Rational Habit Formation: Experimental Evidence from Handwashing in India Reshmaan Hussam Atonu Rabbani Giovanni Reggiani Natalia Rigol

Working Paper 18-030

Working Paper 18-030

Copyright © 2018, 2019, 2020 by Reshmaan Hussam, Atonu Rabbani, Giovanni Reggiani, and Natalia Rigol.

Working papers are in draft form. This working paper is distributed for purposes of comment and discussion only. It may not be reproduced without permission of the copyright holder. Copies of working papers are available from the author.

Funding for this research was provided in part by Harvard Business School.

Rational Habit Formation: Experimental Evidence from Handwashing in India

Reshmaan Hussam Harvard Business School

Atonu Rabbani Dhaka University

Giovanni Reggiani Weiss Asset Management

Natalia Rigol Harvard Business School, Microsoft Research

RATIONAL HABIT FORMATION:

EXPERIMENTAL EVIDENCE FROM HANDWASHING IN INDIA

Reshmaan Hussam∗†, Atonu Rabbani‡,

Giovanni Reggiani§, and Natalia Rigol¶

September 4, 2019

Abstract

We test the main predictions of the rational addiction model, reconceptualized as rational habit formation,in the context of handwashing. To track habit formation, we design soap dispensers with timed sensors.We test for rational habit formation by informing some households about a future change in the returns todaily handwashing. Child weight and height increase for all households with dispensers. Monitoring andincentives raise handwashing contemporaneously, and effects persist well after they end. Anticipation offuture monitoring further raises handwashing: individuals internalize handwashing’s habitual nature andaccumulate stock. Our results inform policy design around the adoption of healthy behaviors. JEL codes:D04, D83, D91, I12.

∗We are indebted to research assistant Sami Safiullah for his excellent field work and project management. We thankthe Birbhum Population Project (BIRPOP) of the Society for Health and Demographic Surveillance (SHDS), a Health andDemographic Surveillance Site in West Bengal, India: in particular, the team of surveyors, survey managers, field monitors, dataentry operators, data managers, and the research team. We are extremely grateful to Nan-Wei Gong, who designed the sensors,as well as AQS, who manufactured them. We received guidance from Esther Duflo, Abhijit Banerjee, Frank Schilbach, BenOlken, Chris Udry, Dean Karlan, Mushfiq Mubarak, Lasse Brune, Hannah Trachtman, David Levine, Vincent Pons, Rafael DiTella, Matthew Weinzierl, as well as helpful comments from conference and seminar participants at UC Berkeley, University ofChicago, MIT, Yale, University of Michigan, UC San Diego, Georgetown University, Columbia University, Delaware University,the Harvard Population and Growth Center, and Harvard Business School. We are grateful for financial support from the J-PALUrban Services Initiative, the Weiss Family Fund, the Schultz Fund, USAID, and the Evenson Fund. Experiment registered inthe AEA Registry under AEARCTR-0000974.†Harvard Business School; corresponding author: rhussam@hbs.edu. (617) 495-6378. Address: Morgan Hall, 15 Harvard

Way, Boston, MA 02163.‡Department of Economics, Dhaka University; atonu.rabbani@du.ac.bd§Weiss Asset Management; giovanni.reggiani@gmail.com¶Microsoft Research and Harvard Business School; nrigol@hbs.edu

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1 Introduction

Habit shapes how man moves in the world. Despite its consideration in economic theory and cognitive

psychology (Marshall 1890; Andrews 1903; James 1914; Pollack 1970; Stigler and Becker 1977; O’Donoghue

and Rabin 2001), however, rarely do economists frame behavior change or technology adoption interventions

around the development of routine, or habit. We focus on a highly consequential real world setting to

test the prevailing economic theory around habit formation - one which thus far has modeled only negative

“addictive” behaviors. Our study utilizes high frequency time-series data to elucidate the temporal dynamics

around the habit-formation process. It then uses the results to inform policy design for the cultivation of

good habits.

Bacterial and viral contamination, resulting in anemia, diarrheal disease, and acute respiratory infection,

kill over two million children per year and severely stunt the growth of millions more. Handwashing with

soap is “the most effective vaccine against childhood infections” (World Bank 2005), reducing person-to-

person transmission and sanitizing the last point of contact between germs and the mouth (Barker et al.

2004; Sanderson and Weissler 1992; WHO 2009). Despite enormous funding in hand hygiene campaigns

over the last thirty years, however, we know little about how to improve hygiene behavior sustainably.

Most interventions find no impact on behavior and/or health (WSP 2012; WSP 2013; Galiani et al. 2015;

Null et al. 2018; Luby et al. 2018). The few that do are intensive omnibus interventions (including

information, resources, monitoring, and other hygiene and sanitation recommendations) that do not generate

clear evidence on the key mechanisms at work and are difficult to replicate (Luby et al. 2005; Bennett, Naqvi,

and Schmidt 2015; Haggerty et al. 1994; Han and Hliang 1989).

One feature of handwashing that may explain the difficulty of sustained change is that the behavior

must be repeated often, and this repetition becomes costly unless routinized. For example, 57% of households

in our sample in rural West Bengal articulate, unprompted, that they do not wash their hands with soap

because “obhyash nai,” or “I do not have the habit.” The need for repetition is not unique to handwashing.

Preventive health behaviors often require routines: water should be treated daily, clean cookstoves used for

each meal, medicine consumed at regular intervals, and handwashing engaged in during the same critical

moments each day. Most of these behaviors suffer low rates of takeup in the developing world despite their

affordability, and neither information provision nor resources appear to generate sustained improvements in

such practices (Dupas and Miguel 2016; Clasen et al. 2014; Kremer and Zwane 2007; Banerjee et al. 2010;

WSP 2012; WSP 2013). Given their repetitive nature and ties to contextual cues, the psychology literature

suggests that such behaviors are ideal candidates for habit formation (Wood and Neal 2007).

In this study, we examine whether handwashing is indeed a habit-forming activity and whether individ-

uals internalize and respond to its habitual nature, as well as explore implications for the design of effective

public health interventions. Motivated by the economic theory of rational addiction (Becker and Murphy

1988), we set up and design an experiment that tests the main implications of this model, overcoming the

identification concerns typical to the literature on rational addiction. Our interventions raise handwashing

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rates by a substantial margin, within eight months translating to improvements in child height-for-age and

weight-for-age of 0.25 and 0.15 standard deviations, respectively.

In order to track the dynamics of habit formation in handwashing, we first develop a novel technology.

In partnership with the MIT Media Lab, we designed a time-stamped sensor technology embedded in a liquid

soap dispenser, which we then manufactured at scale in China at the cost of approximately $25 USD per

dispenser. This technology addresses the challenges faced by all existing handwashing measures: desirability

bias (behavior is self-reported or observed by enumerators), subjectivity (cleanliness is subjectively graded

by enumerators), noise (metrics are broad and data infrequent), and nonspecificity (presence of barsoap,

a common measure, is often due to bathing and laundry rather than handwashing). Our sensor is neither

visible nor accessible to households, yielding objective data; it is precise, measuring use at the second level

and allowing us to connect observed use with critical times of use (such as prior to eating); and it tracks the

use of liquid soap, which is uniquely associated in our study context with handwashing rather than other

cleaning activities.

In our conceptual framework, habit formation is generated by intertemporally linked preferences in

consumption: the more one consumes in the past, the easier consumption is in the present. Intertemporal

complementarities imply that front-loaded (i.e. temporary) interventions, which maximize initial takeup,

can generate a larger stock of consumption - and thereby greater persistence in behavior - than interventions

that are spread over time. This mechanism in turn yields additional predictions given by theory.

In particular, Becker and Murphy (1988), who popularized the theoretical framing of habits (or equiv-

alently, addictive behaviors), posit the theory of “rational addiction.” Rationality implies that agents are

aware of the intertemporal complementarities of a behavior and foresee their future consumption path given

the feature. If a behavior is indeed habit-forming but agents fail to internalize this feature in their con-

sumption decisions, they will underinvest, justifying short-term subsidies to boost usage. Alternatively, if

agents are rational habit formers, an intervention that increases the future value of an activity will generate

a larger habit stock - and thereby more persistence - than one that raises only the present value of the

activity. In its starkest form, a large, one-time incentive to engage in the future will motivate a rational

habit former to engage today (and increasingly so as the future nears), but will have zero effect before the

future arrives on the non-rational habit former. Understanding the nature of the behavior (habitual or not)

and how an agent conceptualizes the behavior (rationally or otherwise) is thus important for the optimal

design of interventions.

In order to generate habit formation, our experimental design must first increase handwashing rates

contemporaneously - a challenge in and of itself as evidenced by existing literature. To do so, we address two

critical features of preventive health behaviors. First, the returns to preventive health behaviors, by virtue of

being preventive, are not salient. Agents’ perceived returns may therefore be lower than the true returns to

the activity. In this setting, incentives that present agents with measurable and immediate returns to good

behavior may be an effective way to increase initial takeup. Second, preventive health behaviors often exist

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outside of social norms: given ubiquitously low takeup, individuals face minimal social costs to shirking.

In this setting, an intervention that monitors activity and thereby invokes social pressure to engage may

activate behavior change.

Our experiment is therefore designed to raise contemporaneous preventive health activity and then test

for the presence of habit formation and rational habit formation. We draw from the psychology literature

and capitalize on our technology to make handwashing amenable to habituation, using the classic habit loop:

a trigger (the evening meal), a routine (handwashing) and a reward (monetary or social incentives) (Duhigg

2014, Aunger et al. 2010, Neal et al. 2015).

Specifically, we distribute handsoap dispensers with liquid soap and sensor technology to a random

subset of households in our sample. Within this group, the experiment has two arms. In the first, we inform

households that we are monitoring their activity with the sensor and provide reports on daily handwashing

performance (a form of social incentives). In the second, we additionally offer daily financial incentives for

handwashing in the form of tickets that are redeemable for household goods. Social and financial incentives

are removed after four months, and we continue to track behavior. Persistence in handwashing after the

withdrawal of incentives is consistent with handwashing being a habit-forming activity. To test for ratio-

nal habit formation, we experimentally vary whether agents anticipate these interventions: to a subset of

households, we announce two months in advance that they should look forward to receiving a monitoring

service or extra daily incentives at a future specified date.1 A present reaction to anticipated changes in

future handwashing confirms that individuals are aware of the intertemporal complementarities between

performance today and performance tomorrow.

We find that, relative to those who receive only a dispenser, monitoring raises short run handwashing

rates by 23%. These higher handwashing rates persist after the withdrawal of the service, suggesting that

handwashing is indeed a habit-forming activity. Additionally, we find compelling evidence of rational habit

formation among households who anticipated the monitoring service: these households wash 39% more

than their non-anticipating counterparts, with the difference increasing as the date of the monitoring service

approaches. It appears, therefore, that households indeed recognize the habit-forming nature of handwashing,

and they act upon this knowledge by accumulating habit stock in preparation for a future rise in the value

of handwashing.

Adding financial incentives to monitoring further increases handwashing rates. Relative to those who

received monitoring only (who wash 45% of the time), those who additionally receive financial incentives

wash 30% more frequently. Relative to those who receive a dispenser only (who wash 36% of the time),

financial incentives raise short run handwashing rates by more than 70%. After incentive withdrawal, higher

handwashing rates persist, substantiating evidence on the habitual nature of the activity. However, these

1Note that all households are notified that the future monitoring service or incentive boost is a possibility at the beginningof the experiment. They are told that resources are limited, so whether or not they should anticipate (receive) these futureboosts will be determined by lottery. If households use the implementing organization’s incentive scheme as a signal of thetrue returns to handwashing, this lottery method equalizes expected value of handwashing as judged by the implementingorganization across anticipating and non-anticipating households.

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effects are not mirrored on the intensive margin of financial incentives: those who experience an increase (in

particular, a tripling) in financial incentives wash only 8% more than their standard incentive counterparts,

suggesting rapidly diminishing marginal returns to financial incentives. This rate decays to the standard

incentive level soon after incentives are withdrawn. Consistent with the small contemporaneous and per-

sistence effects, we find no anticipating reaction to the tripling of incentives: households anticipating this

change wash no more than their non-anticipating counterparts.

Our results are consistent with the key predictions of a model of rational habit formation. When faced

with a future increase in incentives, households choose not to invest in accumulating handwashing stock to

‘prepare’ given the low contemporaneous benefit or prospects of habit formation associated with the change.

On the other hand, households invest considerably in accumulating stock for an intervention with significant

contemporaneous and persistent bite, as evidenced by the monitoring setting.

Lastly, we examine child health outcomes to establish the causal link between handwashing and child

health. We find strong effects on child health, confirming that handwashing alone has substantial returns in

resource-poor settings. Children in households that received a dispenser and soap report 39.5% fewer days

of loose stool (a proxy for diarrhea episodes) and 23% fewer days of acute respiratory infection (ARI) eight

months after distribution (intent-to-treat estimates).2 These effects rise to 74% fewer days of loose stool

and 28% fewer days of ARI when we examine the impact of the treatment on the treated, where ‘treated’ is

defined as those who self-report regularly washing their hands at the eight-month mark.3 These reductions in

morbidity translate to significant improvements in child weight-for-age and height-for-age: treated children

experience a 0.14-0.17 standard deviation increase in their weight-for-age and a 0.23-0.26 standard deviation

increase in their height-for-age (ITT-TOT estimates) eight months after dispenser distribution. The magni-

tude of these effects is comparable to recent nutrient supplementation interventions of significantly greater

intensity and duration (Null et al. 2018, Luby et al. 2018).

This study makes five contributions. First, to our knowledge, this is the first field experiment designed

to test for rational habit formation. Existing empirical studies in rational addiction employ non-experimental

time series data vulnerable to several identification concerns: price instruments are endogenous, consumption

data is self-reported, knowledge of a future change in price is implausible, and serial correlation in prices yields

false positives in favor of rationally addictive behavior (Auld and Grootendorst 2004). Our experimental

design addresses each concern. In a literature that has thus far explored only negative “addictive” behaviors,

this is also the first study to examine rational habit formation in the context of good habits, a key feature

of preventive health behaviors.

Second, this study advances the measurement of habit formation, even apart from the test of rational

addiction. Existing literature typically equates habit formation with long run persistence of temporary

interventions. However, persistence can be due to multiple mechanisms: the purchase of a technology that

2We cannot reject that treatment effects are statistically equivalent across the sub-treatment arms of incentives, monitoring,and dispenser-only, so we report pooled estimates here.

3This measure is correlated with actual dispenser use (correlation of 0.15), which we cannot employ in an IV regression sinceour comparison group of pure control households do not have dispenser use data.

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changes the production function, the process of learning more about an activity such that one updates her

perceived costs or returns to engaging (informational fixed costs), the amplification of one-time behaviors

through social interactions, or the accumulation of consumption stock (Allcott and Rogers 2014; Fujiwara,

Meng, and Vogl 2016). Individual-level habit formation is driven only by the last of these. Importantly, our

evidence of rational habit formation must be due to changes in future consumption stock alone, because we

experimentally vary only the future value of handwashing behavior, not that of health returns. Paired with

an experimental design that includes a dispenser experimentation period across all arms and evidence that

handwashing behavior does not vary with the size of child health returns, we can rule out each alternative

mechanisms and isolate habit formation as the driving force behind persistence in handwashing.

Third, by identifying the marginal impacts of financial incentives, social incentives, and dispenser and

soap provision, this study sets an important precedent for the design of public health campaigns, which

regularly pool interventions and are unable to disentangle the causal effects of each, often theoretically

distinct, dimension of the program. For example, in Luby et al. (2005), a study oft-cited as the hallmark of a

successful handwashing campaign, community volunteers visit households twice weekly, deliver soap, instruct

and monitor households’ handwashing practices, and advise households on other hygiene and sanitation

behaviors. While the authors find a sustained effect of the intervention on child incidence of diarrhea

and respiratory infection, they are unable to identify which aspect of the intervention led to the health

improvements. Our study likewise addresses mechanism conflation in economic incentive interventions: in

any setting in which a conscious principal rewards an agent for performance, a material incentive is a sum of

(1) the material reward and (2) social monitoring and feedback. Particularly in contexts where returns are

not salient and there are no social costs to shirking, it is important to estimate the impact of each mechanism

alone.

Fourth, our data quality is unprecedented within the hygiene and sanitation literature. The objective,

high-frequency data of the dispenser sensors allows us the first opportunity to design an experiment which

disentangles the various behavioral barriers behind low handwashing takeup. This time-stamped data is also

rare in the broader literature of adoption of preventive technologies. It complements the recent collection of

energy conservation studies in developed countries that utilitize household-level meter data from utilities to

examine how various informational interventions affect household energy consumption (Allcott and Rogers

2014; Ito, Ida, and Tanaka 2015; Jessoe and Rapson 2015; Allcott and Kessler 2015, among others). Impor-

tantly, these studies have been unable to link a specific behavioral change to reduced consumption, whereas

the sensor data and design of the present study permit a direct link between increased dispenser use and

handwashing with soap during the evening mealtime.

Finally, this study offers the first treatment on the treated estimate of the impact of handwashing on

child health. In a literature that is plentiful in health impacts of zero, occasional in impacts that are positive

yet unable to identify the cause of improved health, and scarce in causal estimates which still say nothing of

the ratio of input (handwashing) to output (health), this study offers a significant step forward in establishing

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the magnitude of impact that handwashing alone can have on health. This helps us build a more precise

production function of child health as it relates to preventive behaviors in low-resource settings, which is

essential for the more efficient allocation of research and policy funds.

The remainder of the paper proceeds as follows. Section 2 outlines the conceptual framework motivating

our experimental design; Section 3 describes the study sample and experiment; Section 4 specifies our

outcomes of interest and the empirical strategy; Section 5 presents results on handwashing behavior; Section

6 presents results on child health; and Section 7 concludes.

2 Conceptual framework

Our framework for habit formation builds upon the seminal work of Becker and Murphy (1988) on rational

addiction. They and others in their spirit have focused on characterizing and testing the implications

of rational addiction in the context of bad habits. We expand to the context of good habits, of which

handwashing with soap before mealtime is our focus. Substantively, the shift from a bad habit to a good

habit is equivalent to the shift from an activity in which the user experiences positive gains in the present

but incurs costs in the future to an activity in which the user incurs costs in the present but experiences

positive gains in the future. This model is formalized in Section 2.1. Throughout our discussion, we use

‘addiction’ and ‘habit formation’ interchangeably, as their underlying mechanisms are identical.

Intertemporal complementarities in the utility from consumption are an intrinsic property of a habit,

to be experienced by the user by nature of the activity. Rational habit formation (a la Spinnewyn (1981),

and conceptually equivalent to what Becker and Murphy (1988) term rational addiction) is the recognition

of these properties: a rational habit former is one who internalizes the habit forming nature of the activity,

or the craving and tolerance developed through continual engagement, and chooses to engage conditional

on this knowledge. The key tradeoff that a rational habit former faces when choosing whether to engage in

a good habit is therefore between the drop in utility from consumption today and the increase in long-run

utility from the accumulation of the stock in the addictive good.

2.1 Model of rational habit formation

We present a model of rational habit formation for positive behaviors, adapted from O’Donoghue and Rabin’s

(2001) discrete time exposition of rational addiction for bad habits.

Consider a discrete time model with periods 1,...,T. In each period, an agent can wash her hands before

dinnertime such that consumption wt = 1, or refrain from handwashing such that wt = 0. Define kt as the

‘habituation level’ of the agent in period t:

kt = γkt−1 + wt−1, γ ∈ [0, 1) (1)

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Habituation is a recursive function which is dependent on the agent’s habituation to handwashing in

the previous period, kt−1, the level of decay the behavior is subject to, γ, and whether the agent washed in

the previous period, wt−1.

Define the agent’s instantaneous utility function in period t as

ut(wt, kt) =

α− [xt − σkt] if wt = 1

0 if wt = 0

(2)

where α is the health benefit from washing, xt is the net cost associated with handwashing before

dinnertime (in time, effort, attention), and σ is the ease of washing attributable to habituation. Handwashing

is habit forming: the more one has washed her hands in the past, the greater her desire to wash at present

(∂ut

∂kt> 0, or σ > 0).

We wish to maximize the net instantaneous utility of washing:

ut(k) = ut(1, k)− ut(0, k) (3)

= α− xt + σkt

A myopic agent will only wash her hands today if the marginal cost of washing is outweighed by the

health benefit and the benefit from the ease of washing generated by habituation (σ). The more she has

washed in the past, the greater the impact of habituation on the marginal utility of consumption and the

more likely she is to wash in the present. This intertemporal complementarity in consumption is the essence

of habit formation.

xt < α+ σ(γkt−1 + wt−1) (4)

What levers can be shifted to generate a positive desire to handwash? For agents who have not yet

accumulated handwashing stock (most households in our setting), σ offers no leverage, because kt−1 = 0

and wt−1 = 0. To facilitate the accumulation of stock, we must focus first on lowering the net cost of

handwashing, xt. If sufficiently lowered, an agent will wash; she thereby enters period t + 1 with a kt > 0.

If the cost is lowered for a sufficient number of periods, the agent will accumulate enough consumption

stock such that, even absent the subsidy on cost, the desire to engage will be positive. In a setting of habit

formation, subsidies need only be temporary to generate long run behavioral change.

We actualize the reduction in net cost xt in two ways. Our first intervention subsidizes the cost of

daily handwashing by providing daily financial incentives for good behavior. These incentives are provided

by field workers who are members of the communities they survey. In such a context, where incentives are

directly linked to discrete units of behavior and a sentient principal is providing the incentives to the agent

(a setting hardly unique to this study), incentives are implicitly a sum of (1) financial rewards, (2) feedback

on behavior, and (3) the social pressure of being watched and held (financially and/or socially) accountable.

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The latter mechanism can be conceptualized as increasing the cost to shirking. In order to disentangle the

relative importance of the financial reward from the interpersonal cost, we implement both an incentives

intervention and an intervention of feedback sans financial reward, which we term ‘monitoring.’4

Having generated a positive amount of handwashing stock, these interventions can be complemented

with an environment which facilitates maximum retention of handwashing stock. For example, we can

maximize the impact of habituation, σ, by framing the behavior as part of a habit loop: the handwashing

routine can be supported on the front end by the trigger of mealtime and the back end by incentives or

monitoring feedback. Given our limited sample size, we choose not to experimentally vary the type of trigger

administered (it remains the dinner mealtime for all households), but do vary the feedback by providing

households with no feedback, monitoring feedback only, or additionally daily incentives for handwashing

(described in more detail in Section 3.3).5

Thus far we have considered the instantaneous utility function which an agent faces for habit-forming

behaviors. In a world where agents are forward thinking, the long run utility function is as follows:

Ut(kt) = maxwt

[α− xt + σkt] + δUt+1(γkt+1) if wt = 1

δUt+1(γkt) if wt = 0

(5)

where δ ≤ 1 is the agent’s discount factor. A rational habit former is one who recognizes the intertemporal

complementarities in her utility from consumption. If she is aware that her stock of handwashing in the

past affects her likelihood of engaging today, then she is similarly aware that her likelihood of engaging in

the future will be affected by her engagement today. Therefore, if an exogenous shock, such as a drop in the

future cost of handwashing, changes her likelihood of engaging in the future, she should update accordingly

her likelihood of engaging today.

In summary, the model yields the following testable implications.

1. Incentives: ∆wt

∆xt≤ 0. Reducing the cost of handwashing (by increasing the value of handwashing)

raises handwashing rates.

4This framing of financial and social incentives as two means of shifting the net cost of handwashing was established priorto, and directly motivates, the experimental design. We note that we cannot disentangle the value of the feedback itself fromthat of social accountability; to do so would require more sophisticated technology around the sensor, similar to a step-counterfor tracking exercise. However, the sentient principle and agent is a natural setting which activates both mechanisms.

5Our framework abstracts from three features the reader may find in popular models of rational addiction: first, we eliminatehealth internalities, or the multiplicative role of past consumption on present health benefits. Because we do not vary themagnitude of the health returns across treatment arms (which one may have done if public health information were randomized,but we chose to keep this constant across all arms), we do not find this dimension of the framing instructive. Second, we choosenot to incorporate present-biased preferences into our model. This is simple to do following Gruber and Koszegi (2001)or O’Donoghue and Rabin’s (2001) discrete time exposition of the same, but unnecessary for our setting: the goal of theexperiment is to capture whether agents are forward thinking at all, not whether they are fully forward thinking or “100%rational” (O’Donoghue and Rabin 2001). As long as an agent is not 100% myopic, we will detect behavior consistent with [someamount of] rational habit formation. Finally, because we do not vary the trigger, or cue, to handwashing across treatment arms,we choose not to complicate our framework with cue-centered models of habit formation such as that of Laibson (2001); westress however that the motivation behind such models is precisely the reason we focus on the singular activity of handwashingbefore dinnertime, which we encourage across all households. To be sure, we cannot distinguish the role of financial incentivesor monitoring from that of cues, since both types of incentives are attached to dinnertime washing.

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2. Monitoring: ∆wt

∆xt≤ 0. Reducing the cost of handwashing (by increasing the cost of shirking) raises

handwashing rates.

3. Habit formation: ∆wt

∆kt≥ 0. A rise in past handwashing rates increases current handwashing rates.

4. Rational habit formation: ∆wt

∆wt+j≥ 0 with j ≥ 2. A rise in future handwashing rates wt+j ,

for example through an exogenous drop in the future cost of handwashing xt+j , increases current

handwashing rates.6

5. Health: α ≥ 0. Handwashing generates positive health benefits.

2.2 Empirical evidence on rational habit formation

The vast majority of the literature, all of which explores bad habits such as smoking and alcohol consumption,

rests in favor of rational addiction (Becker, Grossman, and Murphy 1991; Chaloupka 1991; Cameron 2000,

Baltagi and Griffin 2002, Gruber and Koszegi 2001). The typical empirical test of rational addiction involves

regressing present consumption on past and future consumption and other demand shifters, instrumenting

for the lag and lead of consumption using the lag and lead of prices or tax rates.

ct =θct−1+βθct+1+δpt + εt

where a positive coefficient θ is evidence of addictiveness and a positive coefficient βθ is evidence of

rational addiction. The ratio of the latter to the former yields the discount rate β (Becker et al. 1994).

However, Auld and Grootendorst (2004) describe the implausible variation in discount rates, unstable

demand, and low price elasticities implied by such literature. They go on to demonstrate that entirely non-

addictive goods such as milk display the same positive and significant coefficient on future consumption as

cigarettes under the standard empirical test, using this supposed rational addictiveness of milk as evidence

for the abundance of false positives in the empirical literature. The authors demonstrate how high serial

correlation in the prices of the commodity of interest and endogeneity in the price instruments can yield a

positive coefficient on future consumption that is incorrectly interpreted as evidence of rational addiction. Of

significant added concern is the implausibility of consumer knowledge of future price changes in the contexts

explored in the literature.

Gruber and Koszegi (2001) seek to address the problems of endogeneity and implausibility of future

changes by employing state specific time trends and using announced but as of yet unenforced tax rate

increases (rather than far future sales data) as instruments for future consumption. This work represents

significant progress vis-a-vis existing literature. However, the context remains vulnerable to the endogeneity

of prices to consumption: taxes may be imposed in regions where demand for cigarettes is declining and

6Note that each of these implications are subject to specific thresholds. Consider the myopic model of habit formation.A reduction in xt to x′t will only shift an individual from not washing to washing today if ∆xt = xt − x′t > xt − [α + σkt].Likewise, for the forward thinking agent, rational habit formation will only shift an agent from not washing to washing todayif ∆δUt+1(γkt+1) = δUt+1(γkt+1)− δUt+1(γk′t+1) > δUt+1(γkt)− δUt+1(γkt+1)− [α− xt + σkt].

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the legislation is therefore more palatable. Furthermore, although the announced tax rate change is an

improvement upon previous work, there is no way to verify whether consumers are aware of the future tax

rate, and the likelihood is low given the year or more between the observed consumption decision and the tax

enactment. These challenges are directly tied to the nature of the non-experimental, aggregate time-series

data employed in existing scholarship.

Our field experiment addresses each concern above. Our design allows us to: (1) impose price changes

exogenously, avoiding endogeneity between prices or tax rates and consumption; (2) explicitly announce

future prices so consumer knowledge is assured; (3) avoid concerns of differential time trends given ran-

domization; (4) avoid endogenous misreporting using our objective measurement device; and (5) avoid the

implications of serial correlation in commodity prices as we impose prices exogenously and randomization

permits us to compare outcomes across groups rather than over time.

3 Experimental Design

3.1 Study sample and context

Our sample population is made up of 2,943 peri-urban and rural households containing 3,763 children below

the age of seven across 105 villages in the Birbhum District of West Bengal, India. Table 1 presents sample

means for a host of household, mother, and child characteristics, as well as measures of the mother’s hygiene

knowledge and practice at baseline. The average mother is just above 30 years old and was married at age

sixteen with six years of education. 55% of households in our sample are day laborers and 20% work in

agriculture. 40% have a latrine, although 68% continue to practice open defecation. Respondents know

a substantial amount regarding hand hygiene: 95% are aware that soap cleans hands, and 79% articulate

without prompting that soap cleans germs. However, hygiene practice is poor. Despite more than 96% of

respondents reporting that they rinse their hands with water before cooking and eating, only 8% report

using soap before cooking and 14% before eating.7 This failure to use soap cannot be due to lack of soap

availability: 99.8% of households report having soap in the home.

Our partner organization, the Society for Health and Demographic Surveillance (SHDS), is a public

health organization with a strong presence in the Birbhum District. SHDS had been conducting a variety of

public health surveys and initiatives within the sample region over the previous ten years. SHDS surveyors

had been visiting all households in our sample biweekly (twice monthly) for one year prior to this study’s

baseline in order to collect child health data, a practice that we continued for the duration of the present

study.

7While these numbers are low, they are likely to be overestimates given self-reporting.

11

3.2 Dispenser and soap features

We employed a standard wall-mounted dispenser as depicted in the top picture of Figure 1, which was

outfitted with a time-stamped sensor. The dispenser is opened with a unique key that was not supplied

to the households during the course of the experiment. Soap was loaded in a one-liter plastic container

inside the dispenser and refilled as needed throughout the course of the experiment during the surveyors’

biweekly visits. The sensor module is fitted between the container and the soap spout, as shown in the

bottom picture of Figure 1. The circuitry is protected by a waterproof casing, an essential feature for the

oft-wet environment of West Bengal and broadly for outdoor environments. Each push of the outer black

button is registered in the sensor, which records the time of each push to the nearest second. The unit is

powered by a small rechargeable 3.7V lithium-ion battery that can last up to two months in the field before

requiring recharging; this was essential given the lack of electricity in many of our rural households. The

sensor is a modular unit, easily removed and refitted into the dispenser; this design permitted surveyors

to easily replace the modules with fully charged versions on their biweekly visit. Each soap dispenser cost

approximately $4 USD, and each sensor module cost approximately $26 USD at a quantity of 1200 pieces;

this cost drops sharply with higher production given the substantial fixed cost of designing the mold for

the waterproof casing. This is the first time-stamped sensor technology to be designed for the purpose of

handwashing in outdoor, off-grid environments and successfully implemented at scale.

The dispenser was installed near the dining space or water station as chosen by the household. Figure 2

depicts a typical setting for the dispenser: families usually eat on a mat on the veranda or just inside the front

door. We chose a wall-mounted dispenser after repeated prototypes of sensor-embedded tabletop dispensers

revealed that (1) the tabletop dispenser was at greater risk of being lost or stolen given its size and mobility,

and (2) creating a permanent ‘handwashing station’ through mounting the dispenser in a prominent place

made it easier for households to remember to wash, potentially enhancing the physical trigger in the habit

loop8. The dispenser was positioned at a height reachable by young children as shown in Figure 3.

Identifying an appropriate soap likewise required extensive piloting. We experimented with several

scents and consistencies to find that households preferred: (1) unscented or lightly scented soap that would

not interfere with their eating experience; (2) soap of a thinner consistency; and (3) soap that lathered easily.

We thus chose a foaming soap with a light scent approved by pilot households. We preserved some scent as

the olfactory system is a powerful sensory source of both memory and pleasure and thus easily embedded

into the habit loop (Duhigg 2012). The foaming soap was both a more pleasant experience for the user and

required less water to lather and wash off; although water availability was not a constraint in our setting

(where water from shallow tubewells is readily available and regularly used before eating), it is a useful

feature for spaces that face water scarcity.

8Pilot households motivated their valuation for the dispenser with the phrase “chokhe pore,” literally meaning that it fallsupon the eyes, making soap use easy to remember.

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3.3 Timeline and treatment groups

Figure 4 provides a map of all treatment arms and the time-contingent randomization process (see Figure 4

at end of paper for a non-abridged version). Henceforth, treatments associated with social incentives will be

referred to as “monitoring”, and those associated with financial incentives will be referred to as “incentives.”

The duration of the experiment, from baseline to final round of handwashing data collection, was August

2015 to March 2017. The randomization was conducted in three stages.9 First, the 105 sample villages were

randomized into Monitoring Villages (MV) and Incentive Villages (IV). Interventions across the villages were

rolled out at the same time. Households in MV were randomized into two groups: (MV0) control and (MV1)

dispenser. Households in IV were likewise randomized into two groups: (IV0) control and (IV1) dispenser

+ incentive. Recall that receiving financial incentives implicitly involves receiving feedback and monitoring.

Monitoring and incentive assignments were first randomized at the village level in order to limit the

scope for inter-household tension: surveyors expressed concern that control households would be angered if

they had some neighboring households who received a dispenser and others who received a dispenser and

incentives. It would be easier to justify the interventions through the limited resources lottery framework if

all dispenser-receiving households within a village received a consistent package of goods (i.e. the dispenser

either always came paired with incentives or never did). This initial-level randomization at the village level

also allowed us to cleanly conduct two parallel rational habit formation experiments (one using monitoring,

the other using incentives), eliminating concern that households anticipating a future change in services

may be confused regarding the type of future change (in other words, households anticipating a future

increase in monitoring could not mistakenly also expect future incentives, since they did not live amongst

any incentivized households).

At rollout, all households received a basic information campaign regarding the importance of washing

hands with soap, especially prior to eating. They also received a calendar with the SHDS logo as a token of

appreciation for participation. They were notified that they would be visited biweekly for one year to collect

information on child health and (for those who received dispensers) check and replenish soap supplies.

The remainder of the randomizations were conducted at the household level, with households in moni-

toring villages and those in incentive villages experiencing a parallel evolution in treatments over time. All

arms were pre-specified prior to the baseline survey. Each treatment arm is described in detail below.

(MV0 and IV0) Control - 1785 HHs: Households were given a simple informational lecture on

the importance of washing hands with soap, with stress placed on the responsibility of the mother to

do so and encourage her household to do so for the sake of her children’s health. They also received a

calendar with the partner organization logo on it as a token of appreciation.

9Given delays in baseline data entry which were outside our control paired with logistical constraints on the interventionroll-out, we performed a one-shot randomization on the household roster without the benefit of stratification along baselinecovariates.

13

Figure 4: Randomization map

(MV1) Dispenser - 130 HHs: Households were given a dispenser, which was described as a high-

quality soap dispenser that would make it easier to wash hands. Households were informed that there

was a switch inside the dispenser that, if turned on, would track their behavior. SHDS wished to offer

a monitoring service to the households in which handwashing would be reported biweekly and tracked

on their calendar. Because resources were limited, the service would be administered by lottery. If

they did not get selected, their switch would not be turned on, their behavior would not be monitored,

and no feedback would be provided.10 Note that in practice, all switches were turned on from the very

beginning, so this practice constitutes deception.

(MV3) Anticipated monitoring - 233 HHs: Two weeks after dispenser distribution, these house-

holds were informed that they had been selected in the lottery: the internal switch would soon be

turned on, and the device would record the time and frequency with which the household washed

their hands with soap.11 The surveyor would be carefully observing this data every two weeks and

would provide the household with a biweekly report of their behavior, particularly around their evening

mealtime, marking the household’s calendar in the presence of the mother. This arm can therefore be

10These lotteries were publicly announced in order to equalize the expected value of the monitoring across receiving andnon-receiving households; it preempted the possibility that a household would update its valuation of handwashing because,for example, the provision of an additional service was a signal that they should value the behavior more.

11Households could choose whether or not they wanted to receive this program; in practice, all selected households chose toaccept it.

14

regarded as a combination of information and feedback, third-party monitoring, and self (or parent-

child/intrahousehold) monitoring. The service would begin two months after dispenser distribution

on a date circled clearly by the surveyor on the household calendar and written on a sticker attached

to the dispenser. This upcoming date was reannounced at each proceeding surveyor visit to ensure

comprehension.

(MV2) Unanticipated monitoring - 119 HHs: Two months after dispenser distribution, these

households were surprised with an identical monitoring service to those in MV3, effective immediately.12

(IV1) Incentives -191 HHs: At the point of dispenser distribution, these households were informed

that there was a switch in their dispenser which, when on, tracked the frequency and time of use; and

that this switch was on and their behavior would be tracked. They were then given a small coin purse

and told that they would receive one ticket for every day in which the device was active during their

stated dinnertime, which they should accumulate in their purse. These tickets could be exchanged for

various household and child prizes as detailed on a prize catalog.13 These incentive payments would

last for four months. Households were also told that SHDS anticipated receiving additional funding

from the government for the project in the near future, at which point SHDS hoped to increase the

reward for handwashing by three-fold. Because the future funds were limited, households would be

entered into a random lottery to see who would receive the future increase in reward. They would be

notified of the results of this lottery within two weeks.

(IV3) Anticipated triple incentives - 310 HHs: Two weeks after dispenser distribution, these

households were informed that they had been selected in the lottery for the incentive boost and could

soon expect to receive triple the number of tickets for every day in which the device was active during

their stated dinnertime for thirty days. The boost would begin two months after dispenser distribution

on a date circled clearly by the surveyor on the calendar and written on a sticker attached to the

dispenser. As in the monitoring scenario, this date was reannounced at each proceeding surveyor visit

to ensure comprehension.

(IV2) Unanticipated triple incentives - 179 HHs: Two months after dispenser distribution, these

households were surprised with an identical incentive boost to those in IV3, effective immediately.

It was important that we provide all [incentivized] households with an incentive from the start of the

experiment in order to establish (1) an understanding of the nature of the incentives such that households

could easily estimate the value of a future boost in incentives and (2) trust between the surveyors and the

12As with the households in MV3, households could refuse to be monitored. In practice, all households accepted the service.13The ideal incentive requires three conditions: (1) the incentive must be divisible; () the daily amount offered must be

sufficiently high to induce behavioral change on a daily basis, which is key to habit formation; and (3) the marginal valueof the units accumulated as the process of habit formation continues must also remain sufficiently high to continue inducingbehavioral change. Tickets exchanged for goods satisfies all three conditions while also offering flexibility in the types of goodsthat a household may find appealing. Prizes were selected to focus on child health and schooling and adult household goods.

15

households that a claimed future increase would indeed by fulfilled.14 These necessities preclude a test

of rational habit formation on the extensive margin for incentives (which would make them more directly

comparable to the monitoring experiment); however, this design most closely mimics the existing literature

on rational addiction, all of which examines future intensive-margin price changes (all significantly smaller

than ours in percentage terms) on current behavior.

Sample sizes were determined around a few constraints: (1) the partner organization had a pool of 2,947

households in their available sample; (2) budget constraints permitted the production of only 1,400 handsoap

sensors and dispensers, of which approximately fifteen percent were reserved as backup (given failure rates

in pilots); (3) we aimed to sample more heavily in incentive villages as we anticipated smaller effect sizes

on rational habit formation from an intensive-margin change in incentives than from the extensive-margin

change in monitoring.

3.4 Identification of effects

The effect of receiving the dispenser and soap alone is captured in the comparison of households in MV1 to

MV0.

A higher takeup of handwashing behavior in MV3 relative to MV1 and IV3 relative to IV1 (before

the price change) demonstrates the presence of rationally habit forming behavior: households who increase

take-up today due to an increase in the future value (or decrease in cost) of handwashing must recognize

that higher take-up today will generate a greater accumulation of the habit stock over time, making it easier

to reap the benefits of the future rewards to the behavior.

A zero difference in take-up between households in MV3 versus MV1 and IV3 versus IV1 prior to the

price change could be due to three reasons: (1) households are not rational habit formers in handwashing;

(2) the future change in the value of handwashing was not sufficiently compelling to induce behavioral

change, even for forward-looking individuals; or (3) handwashing is not a habit-forming activity. The second

possibility is eliminated if households do indeed respond to the price change (i.e. the tripling of tickets or

monitoring service provision) when it is enacted. This contemporaneous effect can be identified by comparing

households in MV1 to those in MV2 and households in IV1 to those in IV2 after the price change, as the

only difference between these sets of households is the price change itself, with no behavioral response

to anticipation. This comparison gives us the pure contemporaneous effect of the incentive boost or the

monitoring service on handwashing behavior.

The third possibility is eliminated by comparing persistence in behavior across all arms after the with-

drawal of all interventions. For households in arms IV1, IV2, and IV3, all incentives [and implicitly, moni-

toring] services were discontinued approximately two months after the price change. For households in arms

MV2 and MV3, all monitoring services were discontinued approximately four months after their introduc-

14These were lessons learned from our pilot, in which we provided future incentives on the extensive margin, and it was clearthat households did not understand what incentives meant or trust that we would provide them until the future date of changearrived and we delivered the tickets.

16

tion.15 In practice, households were informed that the switch in their machine had been “turned off,” that

surveyors would no longer be observing their behavior but would continue to visit monthly to collect child

health data, and that surveyors would no longer provide reports on household handwashing performance

(nor tickets for incentive households).16 A comparison of each treatment arm to MV1 households, who were

never exposed to any interventions beyond the provision of the dispenser and soap, quantifies the extent to

which a handwashing habit was formed due to the temporary incentives or monitoring interventions.17 We

track household handwashing behavior for fourteen months after rollout.

By maintaining the same incentive stream across both groups, a comparison of MV3 to MV2 and IV3

to IV2 over the course of the experiment after the price change allows us to identify the effect of forward

looking, rationally addictive behavior on habit formation (conditional on finding evidence of rational habit

formation prior to the price change). In other words, a long term comparison of take-up between the 3 and 2

groups demonstrates whether forward-looking behavior in fact facilitated the formation of the handwashing

habit.

Finally, comparison of MV2 to IV1 offers the first estimate in the literature of the marginal value of

monetary rewards on top of monitoring and feedback on daily behavior.18 19

15This difference in date of discontinuation was implemented to equalize the exposure of households to each treatment, sinceincentive households had already been receiving incentives for nearly two months prior to the price change.

16As is true for MV1 (dispenser-only) households as well, this practice of informing households that the switch in the machinewas “turned off” constitutes deception. The practice was cleared by IRB boards at both MIT and IFMR (our Indian researchorganization counterpart) prior to implementation and was permitted given the scientific value and significant policy relevanceof the lessons learned. In particular, this practice allows us to estimate the effects of (1) third party monitoring and feedback,yielding a measure of the extent of bias in typical observational outcome measures used in these studies as well as a measureof the role that monitoring effects may play in the cultivation of social norms; and (2) persistence after the withdrawal ofinterventions, yielding a measure of the sustainability of the interventions and the habit-forming nature of handwashing.

17We equate persistence to habit formation under the assumption that persistence is driven purely by the increase in con-sumption stock accumulated through the interventions, not through the acquisition of a technology that shifts households ontoa new hand hygiene path or through learning about the activity or about its returns. These are not trivial assumptions, andwe address each in detail in Sections 5.2 and 6.1.

18Note that the experimental design precludes perfectly capturing the effect of incentives on top of monitoring, although itis quite close. Monitoring was introduced (MV3 and MV2) 60 days after rollout, while incentives (IV2) were introduced imme-diately after rollout. We were deliberate in this choice: monitoring was delayed in order to increase our power on the rationalhabit formation test, with the tradeoff of a loss in the perfect comparison between monitoring only and monitoring+incentivehouseholds. Given the habitual nature of handwashing (or more broadly, dispenser use), the delay in introducing monitoringmay have reduced the malleability of the behavior and therefore the potential effect of the treatment relative to that of incen-tives. This possibility is in fact precisely why we did not delay the introduction of incentives to parallel the introduction ofmonitoring: this would mean a 75 day delay in the introduction of the future price change, reducing the likelihood of finding arational habit formation effect.

19Indeed, this concern is echoed by early economics literature on behavioral change. In describing the law of diminishingutility in his Principles of Economics, Marshall writes: “There is, however, an implicit condition in this Law which should bemade clear. It is that we do not suppose time to be allowed for any alteration in the character or tastes of the man himself. Itis, therefore, no exception to the law that the more good music a man hears, the stronger is his taste for it likely to become; thatavarice and ambition are often insatiable; or that the virtue of cleanliness and the vice of drunkenness alike grow on what theyfeed upon. For in such cases our observations range over some period of time; and the man is not the same at the beginning asat the end of it.”

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4 Methods

4.1 Outcomes of Interest

Our primary outcomes of interest encompass behavioral change in households and child health. We cap-

ture behavioral change through recorded dinnertime-specific daily handwashing rates and recorded total

daily handwashing rates. Note that sensor measures of handwashing rates could only be collected for those

households with dispensers, so we do not have data from the pure control households on these metrics. We

therefore supplement these with alternative measures of hand hygiene commonly employed in the literature.

We collect child health data in the form of self-reported biweekly incidence of child diarrhea and respiratory

illness and anthropometric measures of height, weight, and mid-arm circumference. Each is defined in detail

below.

A. Household handwashing behavior

Handsoap dispenser data was collected every two weeks during surveyor visits. Although it was not possible

to identify the identity of the user at any given press, we proxy for separate users by collapsing presses that

happen two or fewer seconds apart into a single press. In other words, if the device is used in seconds 34, 35,

37, 45, and 46, the first three presses are considered a single use by one household member and the latter two

presses as a single use by another member. Though not exact, observations from pilots elucidated that users

press several times in quick succession and rarely return for more soap during a single handwashing event,

since the water source (usually a bucket right outside the front porch) is not within reach of the dispenser

(unlike the familiar setting of sink, soap, and running water common to more developed contexts).

Mealtime-specific handwashing rates are calculated as the total number of ‘individual’ uses in

the interval of 90 minutes before and after the household’s reported start of the evening meal time. If

a family reported eating dinner every day at 8:00 PM, for example, this outcome would be the sum of

all individual presses observed between 7:00 PM and 8:30 PM.

Binary use at mealtime is derived from the above and is a binary variable which equals one if

at least one ‘individual’ use was observed in the dinnertime interval. This is the outcome by which

we determine calendar markings and tickets earned, and therefore our primary outcome measure of

handwashing at dinnertime. All results presented in the paper utilize this outcome unless specified

otherwise. Results are robust to using the continuous measure and can be provided upon request. 20

Daily handwashing rates are calculated as the sum of all ‘individual’ uses over the course of each

twenty-four hour period.

20We choose this binary measure as our preferred measure of “proper” handwashing because we wanted to minimize Type IIerror in our feedback: we preferred that households were overcompensated for washing than undercompensated due to stricterand less verifiable measures of success (such as “all family members must wash”, which is both harder to achieve and moredifficult to verify), which in turn might diminish treatment effects.

18

Alternative hygiene measures such as direct observation of respondent hand and nail cleanliness,

respondents’ ratings of own handwashing habit formation, and the presence of non-project liquid soap

in the household were collected at the eight-month mark. We also collected measures of household

sanitation, such as whether the household practices open defecation and whether they treat their

water, to explore complementarities in behavior change and alternative mechanisms through which

child health may be affected.

B. Child health

Incidence of child diarrhea and respiratory illness was collected at baseline and again every two

weeks by surveyors, consisting of self-reports in which mothers were asked how many days each child

had experienced diarrhea, loose stool motion, or the symptoms of respiratory illness in the past two

weeks. These survey questions were adjusted at the eight month mark to account for many relevant

cases being excluded given the strict initial definitions (described in detail in Section 6); this cross-

sectional measure at eight months is our primary incidence outcome measure.

Anthropometric outcomes were collected at baseline and again at the eight month mark. These

include child weight, height, and mid-arm circumference as measured by trained surveyors. We sup-

plement self-reported incidence data with anthropometric outcomes to reduce the likelihood that any

observed effects are driven by desirability bias on the part of mothers. Repeated diarrheal disease can

affect child weight and height by reducing a child’s ability to absorb sufficient nutrients from her food

and thereby stunting her growth (McKay et al. 2010). We convert these measures into standardized

height-for-age, weight-for-age, and midarm-circumference-for-age Z-scores (HAZ, WAZ, and MAZ, re-

spectively) using the methodology provided in the WHO anthropometric guidelines; these Z-scores are

calculated (as per WHO methodology) only for children ages 60 months and below (WHO, 2006).

4.2 Temporality of outcomes

Because various interventions were phased in and out at various times, below we define the time period for

each effect of interest.

Baseline period is defined through the baseline survey, which was conducted four months prior to

rollout.

Pre-change (rational habit formation) period is defined as the time between dispenser distribu-

tion and the monitoring service introduction/price change. We also zoom in on the three week period

just prior to the date of change. This is because (1) we showed a video three weeks prior to the date

of change to all dispenser-receiving households in order to increase and standardize comprehension

regarding which treatment group each household was in; and (2) any rational habit formation effect

should increase as the date of the anticipated change approaches.

19

Intervention period is defined as the four month period following rollout for IV1 (single ticket

incentive) households and the four month period following the introduction of the monitoring service

for MV2 (monitoring) households. For IV2 (triple ticket incentive) households only, this period is

defined as the two months following the price change. These are the intervals within which pure

intervention effects can be measured.

Persistence (habit formation) period is defined in the short run and the long run. The short

run examines handwashing behavior within the month after the incentives or monitoring service are

withdrawn; this is chosen to mirror the focused period of rational habit formation prior to the price

change or commencement of the monitoring service. The long run examines handwashing behavior in

the final month of data collection, which is nine months after the incentives are withdrawn (among

IV1 and IV2 households) and seven months after the monitoring service is withdrawn (among MV2

households).

From the start of rollout to the end of the experiment, we accumulate a total of thirteen months of household-

level data on handwashing behavior.

4.3 Empirical strategy

Our preferred specification for our primary behavioral outcomes is as follows:

Washhvt = α+ βTreatmenthvt + δBaselineWashhvt + γt + θv + εhvt (6)

in which Washhvt represents the outcomes specified above, Treatmenthvt is the assigned treatment for

each subset of comparisons described in Section 3, BaselineWashhvt represents the baseline value of the

outcome variable, γt is day fixed effects, and θv is village fixed effects. The latter is included in all but those

regressions comparing treatments across Monitoring and Incentive Villages (we omit village fixed effects in

these regressions since randomization to MV or IV was at the village level). Standard errors are clustered

at the household level except in cross-IV-MV comparisons, in which they are clustered at the village level.

For analyses utilizing the midline survey, which is cross-sectional data collected eight months after rollout,

we omit day fixed effects.

Our preferred specification for our primary child health outcomes is as follows:

Healthcvt = α+ βTreatmentcvt + δBaselineHealthcvt + θv + εhvt (7)

in whichHcvt represents the outcomes specified above, Treatmentcvt is the assigned treatment group specified

in the analysis, BaselineHealthhvt represents the baseline value of the outcome variable, and θv is village

fixed effects. Standard errors are clustered at the household level.21

21A pre-analysis plan is published on the AEA RCT Registry at https://www.socialscienceregistry.org/trials/974/history/7386.

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5 Behavioral results

Table 2 presents a comparison of means between treatment and control households for an extensive set of

baseline characteristics at the household, mother, and child levels. Treatment households are the pooled

sample of all households who received the dispenser and soap; control households are pure control, or

households who received no dispenser or soap. Appendix Table 1 presents the same set of comparisons

for each treatment arm individually. Households are balanced across the majority of observables. Treated

respondents are 0.4 minutes farther from their drinking water source, 3 percentage points less likely to be

Hindu, marry 0.2 years later, rate themselves higher on whether people listen to them but lower on whether

they make their children’s health decisions, have taken their child to the doctor for an illness in the last

two weeks 0.14 times more, and are 3 percentage points and 1 percentage point more likely to have a child

experience a cold or diarrhea in the last two weeks, respectively. While the imbalance on the last three child

health metrics may be concerning, the difference points in the opposite direction of the effects of interest, and

we control for baseline health incidence in all forthcoming health regressions. The disaggregated comparisons

of Appendix Table 1 likewise show no obvious patterns in differences across treatment arms and control,

nor are any of these differences suggestive of imbalance on unobservables in a direction that will lead us to

overestimate our effects of interest.

We next present our main results on the impact of each treatment on handwashing behavior. A note

to the reader: the description of time in all figures and tables henceforth will be relative to the date of

the incentive price change or introduction of the monitoring service, denoted as Day 0. This helps reframe

the experiment to align with the standard field experiment that typically begins when the intervention

commences. In this setting, we begin our experiment 70 days before the key interventions of interest are

implemented, permitting the exploration of whether agents are rational about the [habitual] behaviors they

engage in.

5.1 Main treatment effects

5.1.1 Incentives

Table 3 presents results on the impact of the extensive incentives margin on handwashing behavior by

comparing households in IV2, who received one ticket per day they washed at dinnertime (beginning on the

day of rollout), with households in MV2, who received only the dispenser. Columns 1-4 demonstrate that

incentives worked as intended: after two months of incentives, incentivized households use the dispenser 1.7

more times over the course of the day than control dispenser households (Column 1), but this increase is

Two deviations from the plan should be noted. First, we do not control for willingness-to-pay for the monitoring service (ameasure we elicit at baseline from all those in MV1) in our regressions because field experience made clear that the elicitedvaluations are largely noise. Results are robust to controlling for this value and can be provided upon request. Second,although we intended to cross randomize all dispenser arms with a reminders intervention (involving small alarm clocks placedon top of the dispensers), we never received the clocks due to import complications between Shenzhen and Kolkata, and thushad to eliminate this part of the experiment.

21

not born out during the daytime (Column 2); rather, the bulk of the change in handwashing occurs around

dinnertime (Columns 3 and 4). A similar pattern holds after four months of incentives (Columns 5-8).

Figure 5a plots the raw time trend of handwashing during the daytime and the evening, respectively,

across incentivized and control dispenser households over the four months that households were offered the

one daily ticket incentive. While the response to incentives increases evening handwashing by approximately

one press more per day relative to the control counterparts, there is no parallel trend in daytime handwashing.

A closer look suggests that evening handwashing may first complement and then substitute for daytime

handwashing (with the switch occurring around Day 0), but these differences are not statistically significant.

By and large, households appear to regard each handwashing event as an independent act. Though only

suggestive, this underscores the importance of defining habitual behaviors with precision in behavioral change

campaigns: to “wash hands before dinnertime” is perhaps a more tangible, manageable, and trigger-centric

instruction than the more popular instruction to “wash hands before eating, before cooking, and after

defecation.”

Column 4 and 8 use the preferred binary outcome variable of whether or not the dispenser was active

during the household’s stated dinnertime. Results show that incentivized households are 24 percentage

points more likely than control households to wash at least once during their reported dinnertime, both

after two months (Column 4) and four months (Column 8) of incentives. By the fourth month of incentives,

just before the withdrawal of the intervention, incentivized households are washing their hands during their

reported dinnertime 63% of the time.

Figure 5b plots the time trend of binary dinnertime handwashing rates across incentive and control

households. The dashed vertical lines represent the average dates of surveyor visits, during which incentive

households received markups of their calendars and tickets based on their performance from the last batch of

data collected. The time trend tells an important story. Households were first visited on Day -70: dispensers

were delivered and incentive households were told about their daily ticket rewards, which they would begin

earning immediately. They were next visited on Day -54, during which surveyors collected the first batch of

handwashing data form the dispensers. On the third visit on Day -38, surveyors returned with the results

of the first batch of data and the tickets the household had earned from this batch. Only upon receiving

these tickets did households react to the incentive treatment. The reaction is followed by a steep decay,

which is again buoyed by the next round of surveyor visits and tickets. Each of the third, fourth, and fifth

visits prompt a sharp rise in handwashing, followed by an increasingly shallower decay. By the sixth round,

despite continuing surveyor visits, household performance stabilizes.

This pattern is consistent with two stories. First, households may be building trust in the intervention.

This is likely at the third visit but unlikely by the fifth. A complementary explanation is that surveyor visits

serve as reminders or motivation to engage in handwashing. Motivation is particularly useful (as measured

by the response to the visits) when the stock of handwashing that a household has accumulated is low in the

early rounds. However, it becomes progressively less effective as the stock builds and the behavior becomes

22

habitual. This pattern of “action and backsliding” is replicated in Alcott and Rogers (2014) in the tracking

of household energy usage against the date of letters sent regarding energy consumption; the results are also

consistent with a key prediction of Taubinsky’s (2014) model of inattentive choice and the substitutability

of reminders and habituation.

We next move to the study of rational habit formation. In order to measure rational habit formation,

we must first empirically establish two features of handwashing. The first is that handwashing can be moved

by our chosen interventions of monitoring and incentives, both on the extensive margin and the intensive

margin of an incentive boost. If agents do not respond to these interventions, then the interventions have

failed to change the value of the behavior and agents have no reason to respond to the anticipation of these

interventions. The second feature is that handwashing must be a behavior that can become habitual. If there

exist no intertemporal complementarities in the behavior (measured by persistence after the withdrawal of

interventions), agents gain no utility from accumulating handwashing stock prior to the introduction of the

interventions.

Only after we have examined these two features of handwashing can we consider whether agents are

rational about their habit formation in our setting. We thus present our results from the intervention period

first, then the persistence period, then return to the pre-intervention period to examine evidence of rational

habit formation. Though temporally out of order, this permits a clearer construction of the story we observe.

5.1.2 Intensive margin incentives

We first examine the contemporaneous impact of an intensive-margin shift in incentives on handwashing.

Columns 1 and 2 of Table 4 present the results for the comparison between households who were surprised

with a triple ticket boost in incentives and those who remained with the single ticket incentive at Day 0.

We report results both for the full 60 days during which households were exposed to the boost (i.e. earning

triple tickets), as well as a lagged time frame of Days 30 to 59. The lagged time frame is relevant because

Day 30 is the first day in which households who were eligible for tripled tickets on Day 0 physically received

them. Households respond modestly to the tripling of daily tickets: they wash an average of 2 percentage

points more than their single ticket counterparts over the duration of the triple ticket regime, increasing to

a statistically significant 5 percentage points (8.3%) upon receiving the extra tickets in hand.

Figure 6a plots the three-day moving average of dinnertime handwashing rates for the tripled incentive

arm relative to the standard incentive arm before and after the incentive boost. Note that the regression

results of Table 4 control for the pre-trends evident in the plot.

5.1.3 Monitoring

Columns 3 and 4 of Table 4 estimate the contemporaneous impact of the monitoring service on household

handwashing behavior as compared to dispenser-only households.22 Column 3 presents results for the full

22Recall that the monitoring service lasted from Day 0 to Day 116, which is two months longer than the length of the tripleincentive boost in incentive villages. This was implemented to compensate for the two months of incentives that all incentive

23

tenure of the monitoring service, while Column 4 presents the lagged results of Days 30 to 116. The

monitoring service has a statistically significant and substantial impact on behavior, increasing handwashing

rates by 7.1-8.4 percentage points (21-23%) over the duration of the service provision.

Figure 6b presents the three-day moving average of dinnertime handwashing rates for monitored house-

holds relative to those who received the dispenser only. The graph demonstrates how household behavior

to the monitoring arm reacts most strongly on the day of the first calendar receipt (Day 30), highlighting

the important role of a public feedback mechanism in the effectiveness of the monitoring service. As with

incentives, the regression results in Table 4 control for the pre-trends evident in the plot.

5.2 Persistence

Section 5.1 establishes that the experiment exogenously increased the value and consequently the ‘consump-

tion stock’ of handwashing in each treatment arm, albeit substantially more under the monitoring regime

than the triple ticket regime. This addresses our first and second testable implications: ∂dt

∂xt≤ 0. We now

explore whether this exogenous shift in stock had an impact on subsequent handwashing behavior after the

interventions ceased.

Many studies have examined the role of temporary interventions on persistence of behavior change

(Charness and Gneezy 2009; Conley and Udry 2010; Dupas 2010; Allcott and Rogers 2014; Royer, Stehr,

and Sydnor 2015; Aggarwal, Dizon-Ross, and Zucker 2018; among others). The persistence of temporary

interventions does not readily imply habit formation, however. Persistence can be generated by the purchase

of a technology that changes the production function, the process of learning more about a technology (how

to use it, what the optimal set of inputs is, or what the returns are) such that one updates her desire to

engage, or the accumulation of consumption stock. Habit formation is driven only by the latter. Isolating

this mechanism is a challenge, and existing studies lack the data or the context to distinguish the effects of

consumption stock accumulation from learning or technology acquisition.

In the present study, we can easily rule out the first alternative mechanism behind persistence: because

our outcome measure is the likelihood of dispenser use, it will not capture the effects of any other hygiene-

related technology the household may acquire. Additionally, we find no changes in sanitation or water

treatment practices (see Appendix Section 8.1), suggesting that households do not invest in alternative

technologies that may alter their hand hygiene production function. In contrast, the mechanism of learning

is a greater challenge to address, since the process of engaging in an activity repeatedly generates both

learning about the activity and a growing stock of consumption.

We identify three dimensions of learning that can occur in our context: (1) learning how to physically

wash one’s hands, (2) learning how to use the handsoap dispenser, and (3) learning about the health returns

to handwashing. We argue that the extent of learning required for the washing process is negligible: 99%

households had already received prior to the boost, and thereby permit a closer comparison between the long run effectivenessof incentives relative to monitoring.

24

of households already rinse their hands with water before mealtime, and 100% of households own and thus

are familiar with the use of soap; to combine the two activities should require minimal learning and there

is little reason to expect this to be differential across treatment groups. The extent of learning required

for using the handsoap dispenser, which is a novel technology, may be greater; to address this, we allow

a two-week learning period between the rollout of the dispensers and the assignment to treatment during

which all households can get acquainted with the dispenser. As is evident in Figure 5b, households do indeed

experiment with the dispenser technology for the first ten days, but behavior stabilizes thereafter, suggesting

that this learning is largely complete within the first two weeks prior to treatment assignment.23 Finally,

households may persist in their handwashing because, by washing more, they also learn that handwashing

leads to improvements in health, and therefore update their beliefs on the returns to the behavior. Upon

presenting the child health results in Section 6, we offer evidence that households who experience larger child

health returns are no more likely to persist in their handwashing behavior than those who experience small

child health returns, suggesting that this dimension of learning plays a minimal, if any, role in the persistence

of handwashing behavior.

We therefore interpret persistence in handwashing behavior after the withdrawal of the interventions

as evidence of habit formation: because the interventions that increased consumption stock are no longer

active in this later time frame, any difference in performance between a treatment household and its relevant

control must be due to intertemporal complementarities in the marginal utility of handwashing.

Table 5 presents the results on persistence. Results are separated into the first month after intervention

withdrawal (short run: Panel A) and the final (thirteenth) month of the experiment (long run: Panel

B). Column 1 of Panel A demonstrates that households who previously received the standard incentive

continue to wash their hands during dinnertime 24 percentage points (63%) more than their dispenser-only

counterparts during the first month after incentive withdrawal. The intensive margin of incentives, on the

other hand, has no lasting effect as evident in Column 2 of Panel A: formerly triple-ticketed households

continue to wash their hands slightly more (3 percentage points) than their single-ticketed counterparts

in the month after withdrawal, but this is statistically indistinguishable from zero. Finally, Column 3 of

Panel A demonstrates that, like the incentives on the extensive margin, the stock built from the monitoring

intervention also persists: households are 8.7 percentage points (33%) more likely to wash than their dispenser

control counterparts in the first month after the monitoring service is halted. These results confirm our third

testable implication: ∂dt

∂kt≥ 0.

In the long run, the magnitude of all effects decline. For both the incentives on the intensive margin

and the monitoring service, we see no evidence of persistence nine and seven months (respectively) after

intervention withdrawal (Columns 2 and 3 of Panel B). However, the effect of incentives relative to the

dispenser control remains: households who had received the standard incentive nine months prior continue

23The same features of the behavior apply to handwashing as an experience good: perhaps households learn that soap doesnot ruin the taste of food or dry out their skin as much as they initially feared. The latter is unlikely because householdsregularly use soap in other contexts; the former is unlikely because households are familiar with non-scented soap (in fact, theyrequest it in pilots) that would quickly assuage concerns around taste.

25

to wash 16 percentage points (123%) more than their dispenser control counterparts.24

These snapshots in time mask important trends in handwashing behavior over the seven to nine months

of persistence observation. Figures 7a and 7b present the five-day moving average results for [formerly]

incentivized and monitored households, respectively, relative to the dispenser control. Figure 8 presents

the five-day moving average for all treatment arms, with incentive groups (IV1, IV2, IV2b) pooled and

monitoring groups (MV2, MV2b) pooled. We highlight two observations made plain from this figure. First,

the dispenser control households experience a secular decline in handwashing rates that parallels the decay

of the other treatment arms. We suspect that this may be due in part to an artifact of the experiment:

after the withdrawal of the monitoring intervention, we reduced the frequency of our household visits (for

all households in our sample) from twice monthly to once monthly for the remainder of the experiment.

We sought to be as uninvasive as possible during the persistence period while still preserving access to the

data. A consequence of this may have been a speeding up of the decay in handwashing across all arms.

Second, the behavior of both formerly incentivized and formerly monitored households eventually converges

to that of dispenser control households (approximately 30 days after intervention withdrawal for monitoring

households and 100 days after for incentivized households). While they remain converged for formerly

monitored households, formerly incentivized households more than double their handwashing rates relative

to dispenser control households by Day 230, which corresponds neatly with the arrival of the winter season

in West Bengal. It is likely that the uptick in handwashing reflects a habit that was attached not only to a

time of day but also to a time of year and the associated contextual cues: cold weather, shorter days, and

a visibly higher incidence of ARI symptoms (coughs, colds, and runny noses) in oneself and surrounding

children. Though speculative only, this observation underscores both the value of long term, high frequency

data collection around behavior change (without which we may have assumed permanent convergence) and

the contextual nuances of habit formation.

5.3 Rational habit formation

Having established that handwashing is a habitual activity and that the interventions change, to varying

degrees, the value of handwashing, we now turn to the question of whether agents are rational about the

habit-forming nature of this behavior. Results are presented in Table 6. We first examine the pre-change

period. Recall that during this period, no incentive households had received the tripled tickets and no

[potential] monitoring households had received a monitoring service. Rather, a portion of them had been

notified on Day -54 (two weeks after rollout) that they should expect such a change to take place at a future

24A note on attrition: our sample size declined rapidly over the last several months as sensors malfunctioned. By the finalmonth of data collection, we were left with 255 functional sensors, relative to an initial count of 1140. Appendix Table 2aexplores the relationship between missing data and household handwashing performance: Column 1 presents the difference indinnertime performance over the first nine months of the experiment between households that remained in the sample in thefinal month and those that did not (day fixed effects included); households that remained in the sample perform no better onaverage than their attrited counterparts. Columns 2 and 3 explore whether treatment effects are differential across attritedand remaining households; both coefficients are small, positive, and noisy, suggesting that households remaining in the sampleexperience treatment effects which are no larger than those that attrited. Appendix Figure 1 shows the trend in sensor attrition,which is largely balanced across treatment arms.

26

date as circled on their calendar (Day 0). We compare the behavior of these anticipating households to

households who were not told to expect any change in the future. Results are presented both for the full

period of anticipation (Day -54 to Day -1) as well as for the final three weeks before the date of change (Day

-21 to Day -1).

Columns 1-2 present the results for households anticipating a future tripling of tickets relative to those

who are not. The coefficient of interest is small and imprecise, offering no evidence that anticipation of a

future price change affects current handwashing behavior. In fact, the coefficient becomes smaller as the

date nears the date of change.

Columns 3-4 present the results for households anticipating a monitoring service relative to those who

are not. In contrast to the incentives setting, households anticipating monitoring are 5.2 percentage points

(22.5%) more likely to wash their hands during dinnertime than their unanticipating counterparts; this

rises to a substantial 8 percentage point (39%) difference in the final three weeks before the monitoring

commences.

Table 7 explores whether these patterns continue throughout the rest of the experiment. Columns 1-2

examine the behavior of (now formerly) anticipating households relative to their surprised counterparts over

the course of the triple-ticket or monitoring interventions, and Columns 3-4 examine their behavior after the

withdrawal of the interventions. Consistent with the theory, anticipating triple-ticket households, who accu-

mulated no more stock than their nonanticipating counterparts in the pre-change period, show no differences

in behavior during the triple ticket regime nor after incentive withdrawal. Formerly anticipating households

in the monitoring regime, however, wash 3.9 percentage points (10.2%) more than their surprised counter-

parts (Column 2), decreasing to 0.6 percentage points (3.3%) more on average for all remaining months after

the monitoring service has stopped (Column 4), though neither estimate is statistically significant.

Figures 9a and 9b depict these patterns graphically. Figure 9a plots the five-day moving average of

handwashing behavior between anticipating and nonanticipating triple-ticket households. Household behav-

iors across the two arms follow essentially identical patterns over the course of the experiment. In contrast,

Figure 9b, which plots the same for anticipating and nonanticipating monitoring households, suggests that

the positive effects of the additional handwashing stock accumulated by households anticipating the moni-

toring intervention may have persisted for 200 days.

Lastly, we elicited biweekly forecasts of handwashing to measure the degree of sophistication or intention-

setting households may have regarding their future handwashing behavior. Results are broadly consistent

with actual performance: anticipating households in the monitoring regime intend to wash more prior to the

onset of monitoring, while anticipating households in the triple-ticket regime make no such intention. How-

ever, we interpret the forecasting data with considerable caution given the challenge of eliciting meaningful

forecasts in the field. The results are discussed in detail in the Appendix and reported in Appendix Table 4.

27

5.4 Discussion

Are there competing explanations for why households anticipating the monitoring service responded so sub-

stantially in anticipation, while those anticipating a tripling of tickets did not? One possibility is confusion:

households may have believed that they were being monitored starting on Day -54 rather than Day 0. The

experiment embedded a series of measures to alleviate this concern: first, the future date of change was

circled in red on the household calendar and written on a sticker attached to the handsoap dispenser on Day

-54. Second, households were shown a video on Day -21 reiterating their treatment assignment; the videos

involved comprehension questions where the respondent confirmed the date on which the enumerator would

“turn the switch on” to begin monitoring or incentives would be tripled. Third, households were reminded of

their treatment assignment on every surveyor return date (Day -54, Day -38, and Day -21): as an anticipat-

ing household, one was reminded of the upcoming date of change; as a non-anticipating household, one was

reminded that the surveyor would continue to return every two weeks to collect child health data. Finally, if

households did indeed believe that the monitoring service started on the day of announcement rather than

Day 0, then we should expect their patterns of response to be qualitatively similar to those of households who

actually did receive the monitoring (with no anticipation) on Day 0. However, if we compare the behavior of

MV3.1 to that of MV2.2 (see Figure 9b), we see little in common: anticipating households respond sharply

on visit days and decay nearly as sharply afterwards, while households actually being monitored respond

sharply on visit days and remain responsive, steadily increasing their handwashing rates over time. Although

only suggestive, the two groups are randomly assigned and the difference in patterns is stark and difficult to

reconcile with a story of confusion among anticipating households.25

An alternative argument for why we see a rational habit formation effect among households anticipating

monitoring but not those anticipating triple tickets is one of differential salience. Perhaps the term “moni-

toring” makes the act of handwashing more salient today than the term “tripling of tickets.” (Note that this

is distinct from a salience argument in which being monitored in the future makes handwashing more salient

than receiving triple tickets in the future: if salience from future activity were the mechanism, responding

to such salience would fall within the realm of rational habit formation.) Although there is little one can

do to ensure equal salience of handwashing across related terminology, we offer the following test: on the

days of surveyor visits, salience of handwashing should be maximized regardless of what treatment arm one

is in. Surveyors asked households about the dispenser, how it was functioning, and whether there were any

problems; they asked the household to forecast how many days mothers and children anticipated washing

their hands before mealtime in the coming week; they then [openly] marked the level of soap on the tank to

underscore the importance of soap use, replenished the soap, and performed “maintenance” on (i.e. collected

data from) the dispenser. Indeed, handwashing rates spike in the non-anticipating arm (Figure 9b) on the

25Alternatively, one may think that households were not confused, but simply did not trust us and therefore believed wewere already monitoring them. If this were the case, then come day -54 or -21, when households faced no repercussions tobeing monitored, no feedback, and a continual insistence that a monitoring service would be provided on Day 0, suspicionshould have decreased over time. In contrast, we see a steady rise in responsiveness to the anticipation over time relative tothe non-anticipating control group.

28

visit days. If we interpret these spikes as the effect of maximizing the salience of handwashing, then it is

evident that anticipation of future monitoring has an additional impact on handwashing above and beyond

that of salience alone.26

While confusion, lack of trust, or differential salience may each play some part, various features of our

design and multiple sources of evidence suggest that they are unlikely to be the driving force behind the

results we observe. Our behavioral results instead appear to most closely align with a model of rational

habit formation. While the contemporaneous effects of monitoring were substantial (21% more handwashing

than the relevant control mean), those of the tripling of tickets were small and noisy (4% more handwashing

than the relevant control mean). Similarly, while the persistence of monitoring was clear (essentially zero

decay in the first thirty days), the tripling of tickets had no persistent effects. Consistent with the utility

function of a rational habit former, households chose not to invest in accumulating handwashing stock to

‘prepare’ for an intervention with little contemporaneous benefit ( ∂dt

∂xt≈ 0) or prospects of habit formation

(∂dt

∂kt≈ 0). On the other hand, they invested considerably in accumulating stock for an intervention with

significant contemporaneous and long run bite, confirming our fourth testable prediction: ∂2Ut

∂kt∂kt+1≥ 0.

That households exhibit some detectable level of rational habit formation should be, upon reflection, not

so surprising. First, our design sets up the optimal scenario to facilitate rational habit formation: households

are fully aware that we want to help them develop a habit of handwashing, and we reiterate the future dates

at which the value of the behavior will change. Second, though rational habit formation at first glance

appears to require considerable sophistication, we manifest this behavior in many parts of our lives without

articulating it as such: we train ourselves to eat less, wake up earlier, speak in a particular style, or sit in

a particular manner when we know there is a high-stakes opportunity approaching in which to do so would

reap rewards (or equivalently, save us from punishment). None of these behaviors are ones we must learn

per se (we could, with enough focus, activate them on the spot), but we recognize that practice will make it

easier to engage when the time comes. It appears that handwashing for a community in rural West Bengal

likewise falls in this category: agents internalize, at least in part, the habitual nature of the behavior and

accumulate stock accordingly.

6 Health results

Thus far, we have established that handwashing is a habit-forming behavior and that households in our

sample are sophisticated about its nature. It remains an open question, however, whether the habit of

handwashing is worth acquiring in the high-disease environment of West Bengal, where the marginal value

26The challenge of salience plagues not only most experimental literature in which individuals are responding to various typesof information but also all of the empirical rational addiction literature, where announced future price changes make the currentactivity engaged in more top-of-mind. Existing literature in rational addiction has the compounded salience confound that anexogenous price change may be interpreted as a signal of how valuable or harmful a good is, causing agents to update theircost function and react accordingly. Our experimental design minimizes this confound by making the treatment assignment anexplicit lottery. Our parallel result that the recurring reminder of a future tripling of tickets had zero effect on contemporaneoushandwashing offers further support for the minimal role of salience.

29

of this simple activity may be small given the high exposure to disease from other sources. We now ask:

does handwashing generate positive health benefits, α > 0? We examine three sets of data. The first utilizes

day-level reports by mothers of child diarrhea and acute respiratory incidence (ARI) as collected by surveyors

every two weeks during the first five months of the experiment. We examine health data from months four

and five only, as this encompasses the peak of handwashing performance across treatment households.27

Our second set of outcomes utilizes two-week incidence reports from the midline survey conducted

between months seven and eight. This midline survey revised the manner in which we collected data on

child diarrhea and ARI. The restructuring was motivated by concerns from the field that surveyors were

missing incidence cases. For example, for diarrhea, reporting mothers (1) felt diarrhea was a serious illness

that their children could not suffer from unless the child was visibly sick and (2) often did not know whether

their children had experienced regular loose stool motions since their children played outside most of the day

and defecated in open fields away from the house. We therefore revised the questions to cast a wider net on

illnesses and we required surveyors to have the child present during the time of surveying.28

Our final set of health outcomes comes from the midline survey as well: we recollect anthropometric

measures of child height, weight, and mid-arm circumference.29 We combine these measures with child age

and gender data to create the child’s height-for-age, weight-for-age, and mid-arm circumference-for-age Z-

scores based on guidelines by the World Health Organization (WHO). This analysis is restricted to children

0 to 60 months as specified by the WHO guidelines.30

Table 8a presents the intent-to-treat estimates from the child-day level incidence reports. All regressions

include day and village-level fixed effects as well as a full set of child health baseline controls, although results

are robust to excluding baseline controls (not shown). Columns 1 and 3 report results for the pooled sample

of all treated households relative to households in the pure control group respectively for diarrhea and ARI

incidence. Columns 2 and 4 disaggregate this sample into each treatment group: incentives, monitoring, and

dispenser control households.

27Although this time restriction was not specified in the pre-analysis plan, we did not explore any other time-frame for thehealth outcomes during our analysis to avoid the concern of multiple hypothesis testing.

28The wider net was cast as follows: mothers and children together were asked whether the child had experienced any loosestool motion in the last two weeks. If so, the days they experienced loose stool were recorded. This is in contrast to theprevious five months of incidence data collection, during which mothers (and not children) were asked whether their child hadexperienced loose stool motion at least three times in a day, the clinical definition of diarrhea. Any amount less than three wasnot recorded as an episode. As is evident in Table 8a, this yielded too few cases for statistically significant movement to bedetectable. We acknowledge that a single loose stool motion is not necessarily reflective of diarrhea; however, a single reportedmotion is likely to be a signal for more actual motions in a day (given the recall problem for young children and the lack ofsupervision by mothers). We report the results, however, as ‘loose stool’ and not as ‘diarrhea’ and leave the reader to interpret.For the ARI question, mothers and children together were asked whether the child had experienced any of the symptoms ofARI in the last two weeks, and the surveyor listed the following: runny nose, nasal congestion, cough (with or without sputumproduction), ear discharge, hoarseness of voice, sore throat, difficulty breathing or a prescription from a doctor for such. If therespondent answered yes to any of these symptoms, the surveyor then asked how many days the child had experienced thesesymptoms. This is in contrast to the previous five months, during which surveyors asked whether the child had suffered fromany two of the three symptoms of a runny nose, cough, or fever.

29We had an attrition rate of 9.6 percent in the midline survey. Appendix Table 2b demonstrates that the households surveyedat midline were no different from one another on baseline outcomes across treatment assignment.

30The WHO provides the distribution of each age and gender-specific anthropometric measure for a reference population ofwell-nourished children from Brazil, Ghana, India, Norway, Oman and the United States, such that a Z-score of 0 is the medianof the reference population. We place a special focus on height-for-age as a metric of child health improvement, as linear growthis regarded as the most relevant indicator of overall nutrition (Hoddinott et al. 2013).

30

While estimates for the impact of treatment on diarrhea are consistently negative, they are noisy and

close to zero. This is not surprising, as the reported likelihood of a child in the pure control group suffering

from diarrhea on a given day is only 0.4 percent. Results on ARI are clearer: children in treated households

are 2.2 percentage points (15.3%) less likely to be suffering from ARI on a given day than their untreated

counterparts; this effect size, significant at the one percent level, is relatively evenly distributed across the

treatment groups, with monitoring households seeing the largest drop in ARI incidence of 2.9 percentage

points, or 20.1%.

Table 8b presents the intent-to-treat estimates from the restructured midline survey with and without

baseline controls. Mean two-week incidence of loose stool in the pure control group is 10.4%. A child in a

treated household is 3.2 percentage points (30.4%) less likely to experience loose stool motion in the previous

two weeks. Similarly, the average treated child experiences .08 fewer days of loose stool (39.4%) per two

weeks, significant at the one percent level. When we broaden the net to any loose stool, the impact of

handwashing is clear.

ARI results remain consistent in percent magnitude with those in Table 8a. A child in a treated

household is 3.7 percentage points (13.6%) less likely to show any symptoms of ARI in the last two weeks

and experiences 0.2 fewer days (14.9%) of ARI per two weeks. Appendix Table 3a disaggregates these results

into each treatment arm; treatment effect sizes remain broadly consistent across arms, but we do not focus

on these given concerns over multiple hypothesis testing.

Table 9 presents the intent-to-treat estimates on child anthropometric outcomes. Weight-for-age in-

creases by 0.14 standard deviations, height-for-age increases by 0.23 standard deviations, and mid-arm

circumference-for-age increases by 0.08 standard deviations. To get a sense of the magnitude of these re-

sults, consider that children ages five years and below in treated households are approximately 0.38 kg heavier

than those in pure control households. At a conversion rate of 7780 calories per kilogram (Wishnofsky 1958)

and given that the dispensers have been in use for eight months at the point of data collection, treated

children are able to absorb approximately 12 more calories per day than children without a dispenser.31 Ap-

pendix Table 3b disaggregates these results into each treatment arm, and Appendix Table 3c disaggregates

by age of child. Unsurprisingly, younger children (one to two years of age) benefit most in weight, height,

and mid-arm circumference.

Since the average rate of handwashing at dinnertime among treated households is 47%, we now consider

estimates of the treatment on the treated (TOT). However, because control households were not given

a dispenser, we cannot employ dispenser use as a proxy for handwashing in this instrumental variables

exercise. Instead, we employ two alternative hand hygiene measures we collected across all sample households:

self-reports on whether the mother and child wash regularly (whether they have achieved a handwashing

habit) and enumerator observations of hand cleanliness. Both measures, and especially the self-reports, are

31This exercise was adopted from Bennet et al. (2015), and despite significant differences in the type and time length ofhandwashing interventions being tested between this paper and Bennet et al., the estimated change in per day caloric intakedue to the intervention is remarkably similar (12 v. 14 calories per day).

31

correlated with dispenser use and thus seem like reasonable proxies for handwashing (Appendix Table 5a,

Column 3). For ease of interpretation, we transform both measures into binary variables: the self-report

is equal to one when the respondent articulates that a habit has been achieved and zero otherwise; the

enumerator observation is equal to one when she records clean hands and zero otherwise. We instrument each

with treatment assignment, employing the three treatment groups of incentives, monitoring, and dispenser

households as instruments.

In particular, we run the following two-stage regression for child c in household h, village v, and time t:

Washhv = α+ β1Incentiveshv + β2Monitoringhv + β3Dispenserhv + εhv

Healthchv = α+ β2ˆWashhv + δchv + θv + εchv

in which Washhv is either the self-report or the enumerator observation, δchv is a vector of child health

baseline controls and θv represents village fixed effects.

Table 10 presents the TOT estimates. A child in a household that reports regularly washing at din-

nertime experiences a 59% decrease in the likelihood of having loose stool, a 74% decrease in the number of

days she experiences loose stool, a 24% decrease in the likelihood of experiencing any ARI symptoms, and

27% fewer days of ARI. She also sees a 0.17 standard deviation rise in her WAZ score (noisy) and a 0.26

standard deviation rise in her HAZ score (significant at the ten percent level).

The preceding analysis yields two key takeaways. First, the results provide the first causal evidence

in the literature that handwashing alone generates significant positive health benefits in the developing

world. Second, the analysis highlights that the mere provision of the dispenser and liquid soap has a

significant impact on child health. In fact, the marginal impacts of each treatment arm are for the most

part statistically indistinguishable from the impact of the dispenser arm alone. This large treatment effect

to dispenser provision cannot be due to a newfound availability of soap in treated households, as baseline

estimates point to 99% of households having [and using] soap in the home. Rather, this must be due to some

combination of the household’s valuation of the dispenser and liquid soap and thereby the act of handwashing

(“if we receive something so nice, handwashing must be important and we should use it”) along with the

convenience of the dispenser location, being stationed right next to the place of eating. Novelty is a less likely

explanation, since our results are estimated seven to eight months after the distribution of the machines.

6.1 Learning and child health

Do households internalize these substantial child health returns and increase their valuation of handwashing

(and thereby their handwashing rates in the long run) accordingly? To test the extent to which learning

about the health returns to handwashing generates persistence, we run the following regression separately

for dispenser-only, monitoring, and incentive households:

Persistencecv = α+ β1Healthcv + β2HandwashStockcv + β3BaselineHealthcv + δc + γv + εcv (8)

32

in which Persistencecv is the average handwashing performance during the month following the with-

drawal of incentives or monitoring for child c in village v, Health is a health index constructed using Anderson

(2008) separately for self-reported disease incidence and anthropometric outcomes32, HandwashStock is the

average likelihood of washing during dinnertime over the course of the intervention, BaselineHealth is the

identical incidence or anthropometric index constructed using baseline health variables, δ is a vector of child

and household-level characteristics (sex and age of child, whether child was breastfed exclusively, household

occupation, number of rooms, mother’s age at marriage, and mother’s education) and γ is village fixed

effects. Standard errors are clustered at the household level. A significant and positive β1 coefficient implies

that, conditional on having accumulated the same amount of consumption stock of handwashing, households

that experience larger improvements in health are more likely to persist in their handwashing behavior.33

Appendix Table 9a presents the results separately for each treatment arm and health index type. All

estimates of the coefficient on the health index are statistically insignificant and close to zero. It does

not appear that households are internalizing health gains and updating their handwashing performance

accordingly.

Despite the host of controls for child health and household characteristics, it is possible that learning

effects are washed out by endogeneity in handwashing behavior to household type: households who experience

larger health returns may also be the types of households who handwash little (for example, the sick children

who experience the largest health improvements may reside in poor households - who are on average less

likely to wash than their affluent counterparts - in a manner that is not sufficiently controlled for in our

vector of child and household characteristics). Therefore, we also exploit our panel data on illness collected

during months three through five of the experiment and consider the following exercise: conditional on

households having built the same amount of handwashing stock and experiencing equal levels of sickness,

does a household that experiences an illness the week before a handwashing observation behave differently

from a household that experiences an illness in the week after the observation? Any difference can plausibly

be attributed to the reaction to the health event rather than changes in consumption stock, since the latter

is equivalent across comparison households. To evaluate this, we run the following regression for households

who report an ARI episode in either the week before or after the week of handwashing observation, run

separately for each week of child health panel data34:

Handwashingtcv = α+ β1Sickt−1cv + β2Sick

tcv + β3SickStock

t−1cv + β4HandwashStock

t−1cv + γv + εcv (9)

32We include anthropometric outcomes for completeness, although given the magnitude of effect size, these are likely muchmore difficult for a mother to internalize and learn from than changes in diarrhea and ARI incidence.

33This translates into a learning effect of health returns given two assumptions: first, that the relationship between handwash-ing and health is not one-to-one, but rather there is a random component to the health improvements that a child experiencesfrom a unit of handwashing; and second, that households are unable to separate the random from the direct components ofhealth improvements in their learning process: a household that observes a large child health improvement will attribute thefull gain to handwashing, even if their neighbor accumulates the same amount of handwashing stock and sees only a smallimprovement in child health.

34We examine only ARI outcomes for the panel data given the complications in collecting child diarrhea outcomes prior tothe revised question formatting in the midline survey.

33

In which Handwashingcv is the total number of days the dispenser was used at dinnertime in week t

for child c in village v, Sickt−1 is a binary variable that equals one if the child is sick in the previous week

and zero of the child is sick in the following week, Sickt is a binary variable that equals one if the child is

sick in the current week, SickStockt−1 is the total number of episodes the child experiences from the first

day of observation to the start of the previous week, HandwashStockt−1 is the total number of days the

dispenser was used from the first day of observation to the start of the previous week, and γ is village fixed

effects. Standard errors are clustered at the household level. Our coefficient of interest is β1: a negative and

significant coefficient would suggest that, holding total sickness and handwashing stock constant, children

(households) who experience a sickness in period t−1 devalue handwashing and wash less in period t relative

to those children (households) who experience a sickness in period t+ 1. Conversely, households that remain

healthy in period t−1 learn that handwashing is good for health and therefore wash more in period t relative

to those that remain healthy in period t+ 1.

Appendix Table 9b presents the results. Panel A presents results for households in either the dispenser-

only or the monitoring arms, and Panel B presents results for households in either the dispenser-only or the

incentivized arms. These samples thus correspond to those of the persistence analysis in Table 5 (Panel A).

Over the course of the weeks in which we can observe before, during, and after ARI incidences, no consistent

pattern emerges. Estimates are noisy, with an equal distribution of negative and positive coefficients. It

does not appear that households are - at least coherently or consistently - internalizing the health returns of

their children and updating their valuation and performance of handwashing accordingly.35

Finally and most decisively, note that the rational habit formation effect can only be driven by in-

tertemporal complementarities in the stock of consumption, not by learning about child health effects. This

is because the experiment exogenously increased only the value of handwashing in the future, not that of

the health returns to handwashing in the future.36 Evidence of rational habit formation by households an-

ticipating the monitoring of handwashing behavior therefore offers further evidence that learning about the

health returns cannot be the primary driver of intertemporal complementarities in handwashing. Rather,

the persistence we observe is most likely driven by the accumulation of consumption stock, or the building

of a habit.

35Our test of learning about health benefits is not perfect: perhaps mothers notice more subtle health improvements intheir children that are not captured in our loose stool and ARI metrics. Though possible, we find this unlikely; in ourfield experience, whenever mothers were probed on their comment that the dispenser has made their children healthier, theyconsistently described “healthier” as “fewer coughs, runny noses, fevers, or loose stool.” Given that the health measures wereself-reports, we should have been able to capture perceived changes along precisely these dimensions of health.

36Upon being randomized into receiving the future price change or monitoring service, treatment households face an increasedfuture return to the behavior but, in a world without rational habit formation, identical current returns to the behavior. In thetypical risky technology and learning experiment, one subsidizes current behavior and examines effects on future returns. Inthis study, we subsidize future behavior and examine effects on current behavior, which yields clear evidence of intertemporalcomplementarities, the hallmark of habit formation. It is in this way that the learning and habit formation stories can bedistinguished, and our experimental design identifies only the latter mechanism.

34

7 Conclusion

This study analyzes the process of habit formation in the high-impact preventive health behavior of hand-

washing with soap, examining how individuals internalize and interact with this habit-forming behavior.

Our results suggest that monetary incentives and third-party monitoring and feedback are effective means

of increasing handwashing rates in the short run. While the impact of incentives on the extensive margin is

substantial, intensive-margin changes in incentives have diminishing returns. Both extensive-margin incen-

tives and monitoring have persistent effects, establishing that handwashing is indeed a habitual behavior.

We also present evidence that agents are rationally habit forming: they internalize the intertemporal comple-

mentarities in the marginal utility of handwashing. Specifically, households respond strongly in anticipation

of a future monitoring intervention, but show no response in anticipation of a future intensive-margin change

in incentives. This is consistent with the theory of rational habit formation, in which agents should only

respond in anticipation to interventions that alter the consumption value of future behavior.

This exercise offers the first well-identified estimate of the presence of rational habit formation, and

additionally for good habits, in the literature. These findings inform the optimal incentive design of programs

that seek to increase the takeup of good habits; namely, if a behavior is habit-forming, then an intervention

may do better to front-load incentives, and thereby maximize habit stock, rather than spread incentives over

time. If individuals are rational regarding the habitual nature of the behavior, incentives that are offered at a

future date will generate a larger stock of consumption in the long run than those administered immediately.

The optimal type, size, and length of such incentives remain important areas of future exploration.

This paper also sheds light on the production function for child health as it relates to the input of hand

hygiene. We establish the strong link between handwashing with soap and child incidence of respiratory

infection and diarrhea, and the experiment can uniquely offer treatment-on-the-treated estimates which

suggest that a child who achieved a regular dinnertime handwashing practice saw a 74% decrease in the

number of days she experienced loose stool motion and a 27% decrease in the number of days she experienced

acute respiratory infection. These translate into substantial improvements in anthropometric measures that

have long run implications for the health of the child: receiving a handsoap dispenser and liquid soap

generates, within eight months, improvements in child mid-arm circumference of 0.08 standard deviations,

child weight of 0.15 standard deviations, and child height of 0.23 standard deviations. These findings point

to the importance of human-centric design: dispenser provision was not effective because it provided the

households with soap; rather, the location, ease of use, and attractiveness of the dispenser and soap must

have motivated the practice of handwashing. While this study was not designed to identify these effects, at

the fixed cost of $4.00 USD per dispenser and variable cost of $1.00 USD per 15 liters of foaming soap per

year (the average household consumption rate), such product-design mechanisms are additionally a fruitful

avenue of future exploration.

35

8 Appendix

For Online Publication.

8.1 Household beliefs around handwashing behavior

To examine the degree of sophistication households possess around planned handwashing behavior, we elicited

biweekly forecasts of handwashing: we asked each respondent (mother) to forecast how many days in the

upcoming week she and her children expected to wash their hands with soap before dinnertime. Appendix

Table 4 reports the results. Forecasts offer further suggestive evidence that households for whom the future

service matters (those anticipating being monitored but not those anticipating a tripling of tickets) internalize

the anticipated change in behavior: households anticipating monitoring forecast that they will wash 0.23 more

days (4% more) than their unanticipating counterparts (Columns 1 and 2). We see no such forecasting effect

among anticipating incentivized households. However, note that neither set of households forecasts greater

handwashing rates when the future change arrives relative to those who experience no change (Columns 3

and 4): even monitoring households, for whom we observe a real increase in handwashing relative to their

dispenser control counterparts, do not articulate this change insofar as the forecasting question elicits. It

is possible that these near-zero effects are due to a ceiling effect: the average respondent in the respective

control groups already forecasts washing more than six days in the week; treated respondents cannot forecast

much higher. Finally, Columns 5 and 6 suggest that, at least on the extensive margin of receiving versus not

receiving a dispenser, forecasts appear to be strongly predictive of the truth: those who receive a dispenser

(whether in the incentives, monitoring, or dispenser control treatment arm) forecast washing more than

twice as much as their pure control counterparts. We interpret this forecast data with considerable caution

and minimal weight: forecasts are exceedingly difficult to elicit well given the unusual nature of the question

and the potentially strong experimenter demand effects.

8.2 Alternative measures of household hygiene and sanitation

While the sensor data of dinnertime dispenser use is our primary source of hand hygiene data, we collected

a series of additional observational and self-reported hygiene outcomes that are commonly employed in the

literature. Surveyors observed the cleanliness of respondent hands and nails at the time of survey and graded

each on a three point Likert scale: 0 indicating no visible dirt, 1 indicating some visible dirt, and 2 indicating

extensive visible dirt. This direct observational measure is a popular primary outcome in the handwashing

literature (Bennett, Naqvi, and Schmidt 2015; Ruel and Arimond 2002; Luby et al. 2011; Halder et al. 2010).

However, given the subjective nature of the rating and the fact that surveyors are not blinded to treatment

assignment in this (and most) hygiene experiments, this measure is vulnerable to surveyor bias. If subjects

realize they are being observed (which is not uncommon in practice despite efforts to remain discreet) it

is also subject to observation bias. We also collected respondent ratings on handwashing habit formation.

36

Respondents were asked “Has handwashing with soap before eating become habitual for you?” and were

rated on a five point scale using the following metric: 0 = “How? You did not give us soap”; 1 = “No, not

at all”; 2 = “No, not yet, but it is growing”; 3 = “Yes, mostly, but still needs time”; 4 = “Yes, definitely,

the habit has been established.” Third, surveyors asked the respondent whether they had any liquid soap in

the household; for treated households, the question specified that we were interested in non-project liquid

soap. If households mentally assign barsoap to purposes like bathing and laundry, the presence of liquid

soap may be a signal that handwashing is a household priority. These three hygiene measures were collected

at midline, seven to eight months after rollout. Finally, we proxy for the amount of soap consumed by a

household using the total number of dispenser presses per day.

Results are presented in Appendix Table 5a for pooled and disaggregated treatment arms. Treatment

assignment in the pooled sample is predictive of all alternative hygiene measures. The disaggregated samples

broadly follow the pattern established by our primary hygiene outcome measure of dinnertime dispenser use,

with the incentive arm reflecting larger treatment effects within most measures.37 However, the disaggregated

treatment effects are statistically indistinguishable from one another. These results suggest that alternative,

inexpensive measures of hand hygiene are informative for high-intensity interventions; however, more precise

measurement techniques are essential for identifying the underlying mechanisms behind behavioral change

in handwashing.

We also explore the impact of the interventions on the household’s sanitation behavior. A change

in hand hygiene may be complemented by changes in other sanitation practices, if for example the act of

having handwashing top of mind makes remembering to maintain other preventive health practices easier.

It is also important to examine effects of the interventions on other sanitation outcomes as they affect

our interpretation of the results on child health: improvements in sanitation may be the real cause of

improvements in child health and handwashing merely a correlate. Appendix Table 5b presents the two

household level sanitation outcomes collected during the midline survey: whether the household practices

open defecation and whether they treat their drinking water. Treatment assignment is not predictive of

either of these outcomes: coefficients on treatment are small in magnitude and imprecise, suggesting that

the interventions had no complementary effect on other dimensions of household sanitation.

8.3 Household willingness to pay for soap

Despite the evidence that the intervention lowered the cost of handwashing by making it habitual and

significantly improved child health outcomes, it is ex ante unclear whether households internalize these

impacts of handwashing when making their hygiene and sanitation-related purchasing decisions. One way to

explore this question is through the elicitation of a household’s willingness to pay (WTP) for soap. We play a

37In particular, the incentive effect is half the size of the monitoring effect in the observed hand cleanliness measure; thismay be reflective of the measure’s vulnerability to Hawthorne effects and/or surveyor bias, as monitored households may havebeen more conscious of keeping their hands clean when the surveyor visited, or surveyors may have felt a greater (subconscious)obligation to report cleaner hands among households they monitored

37

WTP game using the Becker-DeGroot-Marschak methodology with households at the eight month mark after

all interventions have been phased out. Respondents (mothers, often with their children accompanying them)

were presented with a series of prizes of increasing value.38 At each level, the respondent was asked whether

she would prefer to take the prize or take a month’s worth of soap.39 To ensure incentive compatibility,

each choice was made in the form of a token and dropped into a bag; after the completion of all choices, the

respondent chose one token at random and received the drawn prize.

Results are presented in Appendix Table 6. Contrary to expectations, treated households value an

additional one month of soap significantly less than control households. A disaggregation by treatment arm

(Column 2) reveals that this difference arises entirely from formerly incentivized households, who express

a willingness to pay that is 18% lower than that of control households. Valuations among monitoring and

dispenser-only arms are statistically indistinguishable from those of pure control. One interpretation of this

result is that the prizes from the incentives intervention gave the mothers (and/or children) a taste for such

rewards which crowded out, rather than complementing, the value of soap. Households may have anchored

their valuation of soap to a negative price as they became accustomed to being paid to use it.

However, formerly incentivized households are also significantly more likely than their pure control

counterparts to have non-project liquid soap in the household (Appendix Table 5a, Column 8), so their lower

valuation may be due to having already established a source for liquid soap once project soap provision ends.

Column 3 therefore excludes all households that report having non-project liquid soap in the household.

Coefficients change only marginally; incentive households still have a 14.5% lower valuation of soap than

control households. Appendix Figure 2 plots the average WTP across each treatment arm for this restricted

sample.

Echoing the results on child health and the absence of learning, this valuation exercise underscores

a problem at the heart of behavioral change in preventive health: health benefits of preventive behaviors

are often too small, too delayed, or too difficult to observe relative to what is required for households to

internalize the causal relationship between behavior and health. Even in a setting where behavioral change

generates health effect sizes that are twenty percent at the lower bound, the household’s decision-makers on

child health do not appear to draw the link between liquid soap provision, the likelihood of handwashing,

and child health outcomes.40 Importantly, the same argument applies to habit formation: despite the

considerable handwashing stock accumulated over eight months and evidence of persistence in handwashing,

households do not increase their willingness to pay for soap. At the point of playing the willingness-to-pay

game, neither the return from habit nor the return to health was sufficiently internalized (or sufficiently

38Because of logistical and contextual concerns, we were not permitted to offer respondents cash. We therefore generated alist of prizes of increasing market value, ranging from Rs. 5 to Rs. 150, which were distinct from the prizes formerly offered toincentive households, and which households, in extensive piloting, could accurately estimate the market value of.

39Respondents were informed that their prize or soap would be delivered to them in six months time. This was a necessarycaveat because treatment households had been promised free soap for one year from rollout; if the soap from the game were tocome during this period, its marginal value would be lower by construction, preventing a valid comparison with pure controlhouseholds.

40This WTP exercise was in fact biased towards finding a higher WTP among treated households: the liquid soap waspresented in a refill pouch, which is more valuable if one has a liquid soap dispenser in the home.

38

high) to shift households’ monetary valuations of soap.41

8.4 Behavioral spillovers

Despite no obvious changes imposed on dispenser-only households throughout the experiment, these house-

holds demonstrate a rise and fall in handwashing rates that closely mimics the pattern of monitored house-

holds (Figure 8). This pattern could be due to parallel time trends, the dispenser control households

undergoing their own process of habit formation, or to spillovers in behavior from neighboring monitored

households.

Because treatment assignment between dispenser-only and monitoring was randomized at the household

level, we capitalize on the random variation in the concentration of monitoring households nearby dispenser-

only households to estimate the size of spillovers in handwashing behavior.42 We choose a radius of one

kilometer around each dispenser-only household, as this is a typical distance within which children play

with one another and attend the same government nursery school, mothers walk to the local pond or road-

side shop, and most conversations are likely to occur. We examine spillovers at three points in time: Day

-40 to -30, when there is little that dispenser households can learn from monitoring households; Day 40

to 50, ten days after monitoring households have received their first calendar (which gives them time to

share their experiences with neighbors), and Day 120 to 130, after monitoring is officially over. If spillovers

drive the rise in rates among dispenser-only households, we should only observe the effects of spillovers

in the middle specification, and potentially remnants in the third specification.43 Results are presented

in Appendix Table 7. Consistent with the prediction, there are zero spillovers in the early part of the

experiment, some evidence of positive spillovers during the peak of discovery in the monitoring regime

(unadjusted for multiple hypothesis testing, the coefficient is significant at the ten percent level), and a

dropoff after monitoring ends. However, the magnitude of these spillovers is modest relative to the upward

trend in handwashing observed among dispenser households over the same time period: at the peak of the

monitoring regime, having one more monitoring household within one kilometer of a dispenser household is

associated with a 1.6 percentage point (5.7%) increase in dispenser household handwashing rates. Thus while

spillovers from monitored neighbors may have played some role in the handwashing behavior of dispenser

households, they can only explain a fraction of the observed rise (nearly a doubling) in handwashing among

dispenser households in the first three months of the experiment.

41Note that our rational habit formation result provides evidence that the effects of habit formation are sufficiently large toaffect behavior ; this, however, appears not to translate into changes in monetary valuation for soap. This could be due to avariety of reasons, such as mental accounting (households allocate a fixed budget to soap/hygiene that is difficult to shift) orprice anchoring (formerly incentivized households anchor their perceived price of soap at a negative value given that they wereeffectively paid to use soap for four months).

42We define concentration of treated households in levels (number of households) rather than percentages because our sampleis far from a complete census of all households in a village, so our denominator would be an ineffective proxy for total numberof neighboring households.

43These time bins were not specified in the pre-analysis plan, but were specified prior to running this analysis; given the largeset of choices one could make in this analysis, alternative time bins were not explored. Alternative distances were explored:0.5 km radius and 2 km radius both yield estimates nearly identical in magnitude, with the former the least precise (resultsavailable upon request).

39

The pattern we observe may alternatively be due to parallel time trends or the natural process of habit

formation. While we cannot rule out the former, habit formation is not unlikely. Consider a habit formation

model in which there exists some fixed amount of consumption stock which must be accumulated before σ

kicks in. This permutation of the model is consistent with the initial shallow decay of handwashing rates in

dispenser control households (Figure 8, Day -70 to 0) followed by their steady rise (Day 0 to 90). Given that

surveyors switched from twice-monthly visits to collect health data to monthly visits to collect data (across

all sample households) around Day 110, which can be regarded as a positive shock to xt, the subsequent

decay in handwashing rates is likewise consistent with the habit formation model. Therefore the pattern of

a secular rise in handwashing rates amongst dispenser households suggests the role of habit formation in

handwashing over time even absent monitoring or incentive interventions.

8.5 Health spillovers

Despite the lack of significant behavioral spillovers, we may expect to see spillovers in health given that

viral and bacterial contamination are the primary sources of diarrhea and ARI morbidity. To measure these

spillovers, we exploit the random variation in the concentration of treated households (pooled) within a one

kilometer radius of pure control households. We run this exercise separately in monitoring villages (MV)

and incentive villages (IV) as households were randomized into pure control and treatment only within these

village categorizations. Appendix Table 8 presents these results. While most coefficients are negative, as one

would expect with positive health spillovers, nearly all are small and imprecise. We find some evidence that

having one additional treated neighbor reduces a pure control child’s days of ARI by 0.03 days and reduces

her likelihood of having ARI symptoms by 0.7 percentage points (2.4%) in monitoring villages (coefficients

significant at the ten percent level, unadjusted for multiple hypothesis testing). Therefore despite substantial

positive health benefits, the habit of handwashing at dinnertime produces modest health externalities for

neighboring children. This is not especially surprising given the timing of the behavioral change we focus

on: while children are most prone to spreading germs during the daytime at school and as they play, our

intervention improves hand hygiene only at night. To maximize positive spillovers, we may want to focus

on hand hygiene interventions linked to schools or a child’s midday meal. This is an important direction for

future research.

40

Figure 1: Soap dispenser anatomy

Notes: The dispenser is a standard wall mounted handsoap dis-penser with a foaming pump. It is opened with a special keyavailable only to the surveyors. The sensor module is securedinside between the pump and the liter container.

41

Figure 2: Typical dispenser location

Notes: An infant sleeps on the verandah of a home. The dispenser is nailed to a wall of the verandah at a heightaccessible by young children. The verandah is the common space for dining.

42

Figure 3: Child using dispenser

Notes: A child uses the dispenser by pushing the black button once or twice. The foaming soap can be rubbedon the hands without water. He then goes to the nearby water pail or tubewell in the courtyard and rinses thesoap off with the help of the mother, who pours the water.

43

44

Fig

ure

4:R

and

omiz

atio

nm

ap

45

Figure 5a: Dispenser use over 24 hours

01

23

4Nu

mbe

r of d

ispen

ser p

ress

es

-70 -40 -10 20 50Day

Dispenser control (MV1.0-1.2)One ticket daily incentive (IV1.0-1.2)

Number of uses in evening (5pm and later)2

46

810

12Nu

mbe

r of d

ispen

ser p

ress

es

-70 -40 -10 20 50Day

Dispenser control (MV1.0-1.2)One ticket daily incentive (IV1.0-1.2)

Number of uses in daytime (before 5pm)

Notes: Figures show the average number of individual presses per day after 5pm andbefore 5pm, respectively. Blue line represents households who received only the dispenser;red line represents households who received the dispenser, feedback, and one ticket forevery night the dispenser was active around their self-reported dinnertime. Day -70 isthe day of rollout.

46

Figure 5b: Binary use at dinnertime

.2.3

.4.5

.6.7

Like

lihoo

d of

usin

g di

spen

ser

-70 -40 -10 20 50Day

Dispenser control (MV1.0-1.2)One ticket daily incentive (IV1.0-1.2)

Likelihood of washing during reported dinner time

Notes: Figure shows the average likelihood of the dispenser being active (at least one press) 1.5 hoursbefore or after the household’s self-reported evening mealtime. Blue dashed line represents householdswho received only the dispenser; red line represents households who received the dispenser, feedback, andone ticket for every night the dispenser was active around their self-reported dinnertime. Vertical dashedrepresent the approximate surveyor visit day. Day -70 is the day of rollout. Tickets were distributed forthe full length of the graph shown (until Day 60).

47

Figure 6a: Incentive effect during intervention regime

.3.4

.5.6

.7Fr

actio

n of

hou

seho

lds

-30 -20 Price change 20 30 40 50 60Day

Standard incentive (IV1.2)3x incentive (IV2.2)

Fraction of households who used at dinner time

Notes: Figure shows the five day moving average likelihood of the dispenser being active (at leastone press) 1.5 hours before or after the household’s self-reported evening mealtime. Blue dashed linerepresents households who received the dispenser, feedback, and one ticket for every night the dispenserwas active around their self-reported dinnertime; red line represents households who received one ticketuntil the point of the “Price change” (Day 0) and received three tickets for every night the dispenserwas active during dinnertime for the remainder of the days displayed in the figure.

48

Figure 6b: Monitoring effect during intervention regime

.1.2

.3.4

.5Fr

actio

n of

hou

seho

lds

-30 -20 Monitoring 20 30 40 50 60 70 80 90 100 110Day

Dispenser control (MV1.2)Monitoring (MV2.2)

Fraction of households who used at dinner time

Notes: Figure shows the five day moving average likelihood of the dispenser being active (at leastone press) 1.5 hours before or after the household’s self-reported evening mealtime. Blue dashed linerepresents households who received the dispenser only; red line represents households who received thedispenser only until the point of the “Monitoring” (Day 0) and received feedback/monitoring on behaviorthereafter for the duration displayed in the figure.

49

Figure 7a: Persistence of incentive effect

0.2

.4.6

.8Fr

actio

n of

hou

seho

lds

25 Incentives stop 125 175 225 275 325Day

Dispenser control (MV1.3)Former standard incentive (IV1.3)Former triple incentive (IV2.3 + IV3.3)

Fraction of households who used at dinner time

Notes: Figure shows the five day moving average likelihood of the dispenser being active (at leastone press) 1.5 hours before or after the household’s self-reported evening mealtime. Blue dashed linerepresents households who received the dispenser only; red line represents households who received thedispenser, feedback, and one ticket until the point of the “Incentives stop” (Day 60), after which theystopped receiving tickets or feedback and therefore became identical to dispenser-only households; greenline represents households who received three tickets until Day 60 and none thereafter.

50

Figure 7b: Persistence of monitoring effect

0.1

.2.3

.4.5

Frac

tion

of h

ouse

hold

s

75 Monitoring stops 175 225 275 325Day

Dispenser control (MV1.3)Former monitoring (MV2.3 + MV3.3)

Fraction of households who used at dinner time

Notes: Figure shows the five day moving average likelihood of the dispenser being active (at leastone press) 1.5 hours before or after the household’s self-reported evening mealtime. Blue dashed linerepresents households who received the dispenser only; red line represents households who received thedispenser and feedback until the point of the “Monitoring stops” (Day 117), after which they stoppedreceiving feedback and therefore became identical to dispenser only households.

51

Figure 8: Time trends across treatment arms

0.1

.2.3

.4.5

.6.7

Frac

tion

of h

ouse

hold

s

-70 -40 -10 20 50 80 110 140 170 200 230 260 290 320Day

Incentives (IV1.3+IV2.3+IV3.3)Monitoring (MV2.3+MV3.3)Dispenser control (MV1.3)

Fraction of households who used at dinner time

Notes: Figure shows the five day moving average likelihood of the dispenser being active (at least onepress) 1.5 hours before or after the household’s self-reported evening mealtime. Green line representshouseholds who received the dispenser only; red line represents households who received the dispenseronly until Day 0 (black vertical dashed line) after which they additionally received feedback/monitoring;blue line represents households who received the dispenser, feedback, and one ticket for every evening thedispenser was active during the evening mealtime. Tickets and feedback were stopped for this group onDay 60 (blue vertical dashed line) and feedback was stopped for the red group on Day 117 (red verticaldashed line).

52

Figure 9a: Rational habit formation in incentives

0.2

.4.6

.8Fr

actio

n of

hou

seho

lds

-70 -40 -10 20 50 80 110 140 170 200 230 260 290 320Day

Anticipation periodUnanticipated 3X tickets (IV1.1)Anticipated 3X tickets (IV3.1)

Fraction of households who used at dinner time

Notes: Figure shows the five day moving average likelihood of the dispenser being active (at least onepress) 1.5 hours before or after the household’s self-reported evening mealtime. Both red and green linesrepresent households who received the dispenser, feedback, and one ticket until Day 0, after which theyreceived three tickets per day the dispenser was active during the evening mealtime; however, greenhouseholds were anticipating the tripling of the tickets while red households were not. The gray boxrepresents the time during which green households were anticipating. Triple tickets then commenced onDay 0 and lasted until Day 60 (third vertical red line).

53

Figure 9b: Rational habit formation in monitoring

0.1

.2.3

.4.5

Frac

tion

of h

ouse

hold

s

-70 -40 -10 20 50 80 110 140 170 200 230 260 290 320Day

Anticipation periodUnanticipated monitoring (MV1.1)Anticipated monitoring (MV3.1)

Fraction of households who used at dinner time

Notes: Figure shows the average likelihood of the dispenser being active (at least one press) 1.5 hoursbefore or after the household’s self-reported evening mealtime. Both red and green lines representhouseholds who received the dispenser only until Day 0, after which they additionally received feed-back/monitoring; however, green households were anticipating the start of monitoring/feedback whilered households were not. The gray box represents the time during which green households were antici-pating. Feedback then commenced on Day 0 and lasted until Day 117 (third vertical red line).

54

Appendix Figure 1: Time trend in attrition of sensor data

.4.6

.81

Frac

tion

of to

tal h

ouse

hold

s

1 2 3 4 5 6 7 8 9 10 11 12 13Month

Dispenser ControlMonitoringIncentives

Fraction of householdsfor whom sensor data was collected

Notes: Figure plots fraction of households in each treatment arm that have sensor data collected overthe course of the experiment.

55

Appendix Figure 2: Willingness to pay for soap

3040

5060

7080

Willi

ngne

ss to

pay

(Rs.

)

Control DispenserMonitoring Incentives

Notes: Figure plots the average willingness to pay (WTP) for soap by treatment arm with standarderrors in gray. Rupee to USD exchange rate is approximately 65:1. WTP was collected eight monthsafter rollout in using a BDM mechanism in which households chose between a one month soap supplyand various household items of increasing (and commonly known) market value.

56

Mean N

Age 31.73 2945Education level 6.03 2945

Hindu 0.72 2945Age at marriage 16.72 2945Daily labor work 0.55 2945Agriculture work 0.21 2945

Number of rooms in house 2.07 2945Deep tubewell used for drinking 55.99 2945

Distance to drinking source 9.44 2945Latrine 0.38 2945

Age (months) 69.43 4829Male 0.50 4829

Height (cm) 104.98 4829Weight (kg) 15.22 4829

# of doctor visits in last two weeks 0.73 4829Had cold in last two weeks 0.37 4829

Had cough in last two weeks 0.08 4829Had diarrhea in last two weeks 0.05 4829

Soap makes hands cleaner than water 94.59 2904Soap prevents sickness 80.33 2903

Soap cleans germs 78.99 2904Cold can spread across people 60.70 2903

Eat with hands 100.00 2903Rinse hands before cooking 96.38 2897

Wash with soap before cooking 8.60 2897Rinse hands before eating 98.83 2900

Wash with soap before eating 13.95 2875Kids wash with soap before eating 30.72 2894

Reason not wash: no habit 57.09 2454Reason not wash: forget 16.87 2454

Wash with soap after defecation 84.84 2857Use soap for bathing 90.41 2898

Open defecation 67.96 2903Has soap in house 99.76 2903

Monthly soap cost (Rs.) 54.12 2903

Mother and household

Child

Hygiene knowledge

Hygiene practice

Table 1. Baseline sample means

57

Pure control mean

Treated mean t-statistic N

Access to electricity 0.954 0.95605 0.261 2,903Daily labor occupation 0.543 0.54975 0.358 2,904Agriculture occupation 0.217 0.20813 -0.572 2,904

Number of rooms 2.066 2.0766 0.208 2,900Deep tubewell drinking source 0.559 0.56624 0.385 2,904

Distance to drinking source (min) 9.268 9.664 1.360 2,901Latrine 0.379 0.37308 -0.322 2,903Mobile 0.770 0.7573 -0.786 2,904

Breakfast start hour 8.028 8.072 0.803 2,893Lunch start hour 12.92 12.9601 1.193 2,893Dinner start hour 20.37 20.3809 0.300 2,901

Cold can spread 0.611 0.60178 -0.311 2,903Soap cleans germs from hands 0.945 0.94684 0.216 2,904

Number of times hands washed 2.701 2.6876 -0.718 2,904Open defecation practiced 0.683 0.67485 -0.460 2,903

Age (years) 31.67 31.82 0.448 2,908Education (years completed) 6.017 6.0422 0.156 2,906

Hindu 0.727 0.6978 -1.699 2,903General caste 0.336 0.3576 1.196 2,899

Age at marriage 16.41 16.658 2.567 2,885People listen 3.001 3.0491 1.504 2,902

Mother makes child health decision 3.352 3.193 -2.227 2,898

Age of child (months) 69.48 69.336 -0.196 4,829Male child 0.500 0.4952 -0.303 4,835

Height (cm) 104.8 105.261 1.022 4,821Weight (kg) 15.22 15.1876 -0.187 4,820

Preventive check up (no. of times 6 mo.) 0.756 0.7 -0.840 1,748Sick doctor visit (no. of times 6 mo.) 1.659 1.798 1.364 1,703

Had cold in last two weeks 0.355 0.3852 1.814 4,827Had cough in last two weeks 0.0757 0.08474 0.992 4,771

Had diarrhea in last two weeks 0.0478 0.0584 1.414 4,832Exclusively breastfed (no. of months) 4.698 4.6078 -0.556 3,211

Table 2. Balance across treated and control

Mother

Household

Hygiene and

sanitation

Children below eleven years

Notes: “Treated” pools all households that received a dispenser. “Pure control” are households who did not receive adispenser. t-statistics computed in a regression of the variable on treatment assigment with village level fixed effects.

58

59

60

61

62

63

Table 8a. Daily child diarrhea and ARI outcomes, ITT estimates(1) (2) (3) (4)

Treated household -0.000866 -0.0222***[0.000718] [0.00575]

Incentive -0.000268 -0.0183**[0.000897] [0.00710]

Monitoring -0.00214* -0.0292***[0.00127] [0.0107]

Dispenser only -0.00141 -0.0288**[0.00156] [0.0146]

Mean of pure control 0.00448 0.00448 0.144 0.144[0.000455] [0.000455] [0.00361] [0.00361]

Observations 129,410 129,410 129,410 129,410

Whether child had ARIWhether child had diarrhea

Notes: Observations at the child-day level. All regressions include day and village fixed effects and the following baseline child health controls: child age, child sex, baseline height, baseline weight, baseline mid-arm circumference, whether the child had a cold in the two weeks prior to baseline, whether the child had a cough in the two weeks prior to baseline, whether the child had diarrhea in the two weeks prior to baseline, and the number of months the child was breastfed. Biweekly child health data spans February and March of 2016 (4-5 months after rollout). All treatment effects are estimated relative to the pure control group. Robust standard errors in brackets and are clustered at the household level. *** p<0.01, ** p<0.05, * p<0.1.

64

Table 8b. Preferred diarrhea and ARI measures at eight months, ITT estimates(1) (2) (3) (4)

Treated household -0.0230** -0.0315*** -0.0575** -0.0817***[0.00849] [0.00975] [0.0208] [0.0236]

Mean of pure control 0.100 0.100 0.209 0.209[0.00572] [0.00572] [0.0151] [0.0151]

With baseline controls X XObservations 4,940 3,820 4,955 3,830

(5) (6) (7) (8)

Treated household -0.0281** -0.0393** -0.163** -0.204**[0.0138] [0.0154] [0.0770] [0.0884]

Mean of pure control 0.270 0.270 1.247 1.247[0.00886] [0.00886] [0.0504] [0.0504]

With baseline controls X XObservations 4,955 3,830 4,955 3,830

Notes: Observations are at the child level. Sample includes children younger than fourteen years. Data was collected seven to eight months after rollout. "Treated household" is any household that received a dispenser (the pooled sample of incentive, monitoring, and dispenser only households). "Whether child showed any ARI symptoms" equals one if the child experienced any of the following in the two weeks prior: runny nose, nasal congestion, cough (with or without sputum production), ear discharge, hoarseness of voice, sore throat, difficulty breathing or a prescription from a doctor for such. Baseline controls include: child age, child sex, baseline height, baseline weight, baseline mid-arm circumference, whether the child had a cold in the two weeks prior to baseline, whether the child had a cough in the two weeks prior to baseline, whether the child had diarrhea in the two weeks prior to baseline, and the number of months the child was breastfed. Robust standard errors are in brackets and are clustered at the household level. p-values adjusted for multiple hypothesis testing using Anderson (2008). *** p<0.01, ** p<0.05, * p<0.1.

Total days of ARI in last two weeks

Total days of loose stool in last two weeks

Whether child showed any ARI symptoms in last two

weeks

Whether child had any loose stool in last two weeks

65

Table 9. Child anthropometric outcomes after eight months, ITT estimates(1) (2) (3) (4) (5) (6)

Treated household 0.145* 0.135* 0.217* 0.227* 0.0991* 0.0752*[0.0766] [0.0640] [0.101] [0.0902] [0.0603] [0.0518]

Mean of pure control -2.167 -2.167 -1.866 -1.866 -1.365 -1.365[0.0459] [0.0459] [0.0666] [0.0666] [0.0432] [0.0432]

With baseline controls X X X

Observations 945 863 944 862 940 858

Weight-for-age z-score

Height for age z-score

Mid-arm circ. for age z-score

Notes: Observations are at the child level. Height-for-age z-score (HAZ), weight-for-age z-score (WAZ), and midarm circumference-for-age z-score (MAZ) are calculated using WHO anthropometric methodology. Sample is limited to children 60 months and younger and excludes children with implausible z-scores as pre-specified in the WHO methodology. Data was collected seven to eight months after rollout. "Treated household" is any household that received a dispenser (the pooled sample of incentive, monitoring, and dispenser only households). Baseline controls include: child age, child sex, baseline HAZ baseline WAZ baseline MAZ, whether the child had a cold in the two weeks prior to baseline, whether the child had a cough in the two weeks prior to baseline, whether the child had diarrhea in the two weeks prior to baseline, and the number of months the child was breastfed. Robust standard errors are in brackets and are clustered at the household level. p-values adjusted for multiple hypothesis testing using Anderson (2008). *** p<0.01, ** p<0.05, * p<0.1.

66

67

Tabl

e 10

. Chi

ld h

ealth

out

com

es, T

OT

estim

ates

(1)

(2)

(3)

(4)

(5)

(6)

(7)

Whe

ther

ch

ild h

ad

any

loos

e sto

ol in

last

two

wee

ks

Tota

l day

s of

loos

e sto

ol in

last

two

wee

ks

Whe

ther

ch

ild

show

ed

any

ARI

sy

mpt

oms

in la

st tw

o w

eeks

Tota

l day

s of

ARI

in

last

two

wee

ks

Wei

ght f

or

age

z-sc

ore

Hei

ght f

or

age

z-sc

ore

Mid

-arm

ci

rc. f

or

age

z-sc

ore

Regu

larly

was

hes (

self

repo

rt)-0

.059

1***

-0.1

54**

*-0

.065

2**

-0.3

35*

0.17

20.

262*

0.09

91[0

.019

4][0

.046

0][0

.029

5][0

.172

][0

.109

][0

.148

][0

.085

5]

Han

ds o

bser

ved

clea

n-0

.484

*-1

.451

**-0

.519

-2.8

840.

650

0.67

50.

287

[0.2

63]

[0.6

94]

[0.3

47]

[2.0

52]

[0.9

04]

[1.3

36]

[0.6

30]

Mea

n of

pur

e co

ntro

l0.

100

0.20

90.

270

1.24

7-2

.167

-1.8

66-1

.365

[0.0

0572

][0

.015

1][0

.008

86]

[0.0

504]

[0.0

458]

[0.0

665]

[0.0

432]

Obs

erva

tions

3,81

43,

824

3,82

43,

824

861

860

856

Not

es: O

utco

me

data

was

col

lect

ed se

ven

to e

ight

mon

ths a

fter r

ollo

ut. Z

-sco

res i

n co

lum

ns 5

-7 a

re c

alcu

late

d us

ing

WH

O a

nthr

opom

etric

met

hodo

logy

. Sam

ple

in c

olum

ns 5

-7 is

lim

ited

to c

hild

ren

60 m

onth

s and

you

nger

and

exc

lude

s ch

ildre

n w

ith im

plau

sible

z-s

core

s as p

re-s

peci

fied

in th

e W

HO

met

hodo

logy

. Sa

mpl

e in

col

umns

1-4

incl

ude

child

ren

youn

ger t

han

four

teen

. Reg

ress

ion

show

s the

trea

tmen

t on

the

treat

ed e

stim

ates

whe

re "t

reat

ed" i

s eith

er (1

) a h

ouse

hold

w

ho re

ports

was

hing

han

ds re

gula

rly d

urin

g di

nner

time,

or (

2) a

hou

seho

ld w

hose

resp

onde

nt h

as c

lean

han

ds a

s jud

ged

by th

e en

umer

ator

, bot

h of

whi

ch a

re in

strum

ente

d fo

r by

each

of t

he th

ree

treat

men

t gro

ups (

ince

ntiv

es, m

onito

ring,

and

di

spen

ser).

"Whe

ther

chi

ld sh

owed

any

ARI

sym

ptom

s" e

qual

s one

if th

e ch

ild e

xper

ienc

ed a

ny o

f the

follo

win

g in

the

two

wee

ks p

rior:

runn

y no

se, n

asal

con

gesti

on, c

ough

(with

or w

ithou

t spu

tum

pro

duct

ion)

, ear

disc

harg

e, h

oars

enes

s of

voic

e, so

re th

roat

, diff

icul

ty b

reat

hing

or a

pre

scrip

tion

from

a d

octo

r for

such

. A

ll re

gres

sions

incl

ude

the

follo

win

g ba

selin

e co

ntro

ls: c

hild

age

, chi

ld se

x, b

asel

ine

heig

ht, b

asel

ine

wei

ght,

base

line

mid

-arm

circ

umfe

renc

e, w

heth

er th

e ch

ild h

ad a

col

d in

the

two

wee

ks p

rior t

o ba

selin

e, w

heth

er th

e ch

ild h

ad a

cou

gh in

the

two

wee

ks p

rior t

o ba

selin

e,

whe

ther

the

child

had

dia

rrhea

in th

e tw

o w

eeks

prio

r to

base

line,

and

the

num

ber o

f mon

ths t

he c

hild

was

bre

astfe

d.

Robu

st sta

ndar

d er

rors

are

in b

rack

ets a

nd a

re c

luste

red

at th

e ho

useh

old

leve

l. p-

valu

es a

djus

ted

for m

ultip

le h

ypot

hesis

te

sting

usin

g A

nder

son

(200

8). *

** p

<0.0

1, *

* p<

0.05

, * p

<0.1

.

68

69

App

endi

x Ta

ble

1. B

alan

ce c

ompa

rison

s for

disa

ggre

gate

d tre

atm

ents

Varia

ble

Cont

rol

Ince

ntiv

est-s

tat

NCo

ntro

lM

onito

ring

t-sta

tN

Cont

rol

Disp

ense

r t-s

tat

NEl

ectri

city

0.95

30.

95-0

.111

1,93

30.

955

0.95

967

0.37

385

40.

955

0.97

0.88

163

4D

aily

labo

r0.

534

0.55

0.74

71,

934

0.56

70.

5628

5-0

.128

854

0.56

70.

4991

-1.3

8363

4A

gric

ultu

re0.

224

0.22

-0.4

881,

934

0.20

00.

2056

0.22

385

40.

200

0.20

763

0.22

063

4N

o. o

f roo

ms

2.15

12.

190.

636

1,93

11.

848

1.91

570.

909

853

1.84

81.

965

1.05

963

3D

TW d

rinki

ng0.

549

0.54

-0.4

431,

934

0.58

50.

6133

1.46

885

40.

585

0.55

67-0

.981

634

Dist

ance

to so

urce

8.99

09.

361.

297

1,93

39.

976

9.97

389

-085

29.

976

10.3

840.

541

633

Latri

ne0.

361

0.32

-2.0

061,

933

0.42

50.

4484

0.77

185

40.

425

0.47

741.

192

634

Mob

ile0.

773

0.75

-1.3

021,

933

0.76

20.

7742

0.42

185

50.

762

0.80

331.

034

635

Brea

kfas

t tim

e8.

049

8.07

0.51

61,

924

7.97

78.

091.

970

851

7.97

78.

151

2.07

763

1Lu

nch

time

12.9

012

.94

1.09

41,

924

12.9

712

.963

8-0

.171

851

12.9

712

.984

30.

231

631

Din

ner t

ime

20.3

820

.37

-0.2

521,

931

20.3

420

.416

11.

221

852

20.3

420

.342

560.

0381

632

Cold

can

spre

ad0.

628

0.62

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061,

933

0.56

80.

5785

0.23

385

50.

568

0.58

210.

212

635

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cle

ans g

erm

s0.

945

0.94

-0.0

461

1,93

40.

945

0.94

249

-0.1

9185

50.

945

0.94

986

0.28

263

5Ti

mes

han

dwas

h2.

743

2.74

-0.0

608

1,93

42.

594

2.62

491.

025

855

2.59

42.

6312

0.94

463

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pen

defe

catio

n0.

697

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01,

934

0.64

80.

623

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0085

40.

648

0.58

5-1

.392

635

Age

(yea

rs)

31.7

131

.70

-0.0

320

1,93

431

.58

32.3

461.

548

855

31.5

831

.46

-0.1

8463

5Ed

ucat

ion

(yea

rs)

5.97

45.

67-1

.551

1,93

36.

128

6.46

21.

179

854

6.12

86.

819

1.66

363

4H

indu

0.77

20.

77-0

.093

91,

933

0.61

30.

6242

0.63

685

40.

613

0.54

5-2

.595

634

Gen

eral

cas

te0.

291

0.26

-1.4

321,

930

0.45

00.

4671

0.62

585

30.

450

0.54

742.

471

633

Age

at m

arria

ge16

.33

16.4

20.

824

1,92

216

.61

17.0

442.

519

847

16.6

116

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0.92

063

0Pe

ople

liste

n2.

987

3.02

0.85

31,

933

3.03

43.

0867

0.90

585

43.

034

3.02

21-0

.162

635

Child

hea

lth d

ec.

3.47

73.

35-1

.580

1,93

03.

036

2.97

38-0

.509

853

3.03

63.

0113

-0.1

4463

4

Child

age

(mo.

)69

.88

69.0

9-0

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3,22

568

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69.9

1.05

71,

406

68.5

069

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0.58

91,

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e ch

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0.50

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491

0.50

60.

505

1,40

60.

491

0.45

53-0

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1,07

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eigh

t (cm

)10

5.2

105.

14-0

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3,22

110

3.8

105.

385

1.82

41,

403

103.

810

5.33

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21,

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Wei

ght (

kg)

15.3

515

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913,

221

14.9

215

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0.71

31,

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14.9

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k up

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t (#)

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ck v

isit (

#)1.

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1.61

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737

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533

382

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0.33

70.

361.

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670.

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84-0

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406

0.05

670.

0686

0.56

61,

070

Brea

stfed

(mo.

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525

4.71

0.99

12,

170

5.13

74.

542

-2.2

5790

65.

137

4.52

9-2

.369

687

Hou

se-

hold

Hyg

iene

an

d sa

nita

tion

Child

ren

belo

w

elev

en

year

s

Mot

her

70

71

72

73

74

Appendix Table 2. Attrition trends (1) (2) (3)

VARIABLES

Attrited v. remaining sample -0.0214 -0.0448 -0.0832[0.0146] [0.0500] [0.0595]

Monitoring treatment effect - attrited v. remaining sample 0.0415[0.0506]

Incentive treatment effect - attrited v. remaining sample 0.0601[0.0625]

Constant 0.767*** 0.303*** 0.293***[0.0316] [0.0674] [0.0686]

Observations 239970 96472 169912

Whether household used at dinner time (0-9 months)

Notes: Observation at the household-day level. All regressions include village and day level fixed effects. "Remaining sample" is made up of the households who did have sensor data collected in the last month of the experiment; "Attrited sample" is made up of those that did not. Outcome variable is a binary variable that equals one if the household used the dispenser during dinner time and zero otherwise; these outcomes are drawn from the first nine months of the experiment. Robust standard errors in brackets and clustered at the village level. *** p<0.01, ** p<0.05, * p<0.1

75

Appendix Table 2b. Attrition trends for midline survey

76

Appendix Table 3a. Child health after eight months disaggregated by treatment arm (1) (2) (3) (4)

Whether child had any loose stool in last two weeks

Total days of loose stool in

last two weeks

Whether child showed any

ARI symptoms in

last two weeks

Total days of ARI in last two weeks

Incentives -0.0267** -0.0726** -0.0225 -0.138[0.0125] [0.0297] [0.0195] [0.108]

Monitoring -0.0333** -0.0971** -0.0572** -0.287*[0.0169] [0.0407] [0.0276] [0.169]

Dispenser only -0.0586*** -0.100* -0.102*** -0.421*[0.0219] [0.0567] [0.0363] [0.228]

Mean of pure control 0.100 0.209 0.270 1.247[0.00572] [0.0151] [0.00886] [0.0504]

Observations 3,820 3,830 3,830 3,830Notes: Observations are at the child level. Data was collected six to seven months after rollout. "Whether child showed any ARI symptoms" equals one if the child experienced any of the following in the two weeks prior: runny nose, nasal congestion, cough (with or without sputum production), ear discharge, hoarseness of voice, sore throat, difficulty breathing or a prescription from a doctor for such. All regressions include the following baseline controls: child age, child sex, baseline height, baseline weight, baseline mid-arm circumference, whether the child had a cold in the two weeks prior to baseline, whether the child had a cough in the two weeks prior to baseline, whether the child had diarrhea in the two weeks prior to baseline, and the number of months the child was breastfed. Robust standard errors are in brackets and are clustered at the household level. *** p<0.01, ** p<0.05, * p<0.1.

77

(1) (2) (3)

Weight for age z-score

Height for age z-score

Midarm circ. for age

z-score

Incentives 0.114 0.192* 0.00801[0.0788] [0.102] [0.0599]

Monitoring 0.181 0.295 0.172*[0.122] [0.181] [0.103]

Dispenser only 0.143 0.269 0.250*[0.180] [0.325] [0.137]

Mean of pure control -2.167 -1.866 -1.365[0.0459] [0.0666] [0.0432]

Observations 863 862 858

Notes: Observations are at the child level. Dependent variables calculated using WHO anthropometric methodology. Sample is limited to children 60 months and younger and excludes children with implausible z-scores as pre-specified in the WHO methodology. Data was collected eight months after rollout. Baseline controls are included in all regressions and consist of: child age, child sex, baseline HAZ, baseline WAZ, baseline MAZ, whether the child had a cold in the two weeks prior to baseline, whether the child had a cough in the two weeks prior to baseline, whether the child had diarrhea in the two weeks prior to baseline, and the number of months the child was breastfed. "Incentives" is the pooled sample of all households in the standard incentive arm, surprised three ticket arm, and anticipated three ticket arm. "Monitoring" is the pooled sample of all households in the surprised monitoring arm and anticipated monitoring arm. Robust standard errors are in brackets and are clustered at the household level. *** p<0.01, ** p<0.05, * p<0.1.

Appendix Table 3b. Child anthropometric outcomes after eight months disaggregated by treatment arm

78

Appendix Table 3c. Child anthropometric outcomes after eight months disaggregated by age

Age in months at rollout 1-12 13-24 25-36 37-48 49-60

Panel A

Received dispenser -0.0966 0.114 0.283* -0.135 0.236(0.254) (0.252) (0.157) (0.123) (0.251)

Constant -2.070 -0.790 -1.785 -1.809 -1.108(0) (0.330) (1.719) (0.133) (1.559)

Observations 104 178 206 271 103

Panel B

Received dispenser -0.0869 0.195 0.304* 0.0384 -0.00498(0.469) (0.403) (0.179) (0.154) (0.397)

Constant -1.280 -0.200 -0.397 -1.542 0.621(2.26e-07) (0.779) (1.299) (0.151) (1.837)

Observations 104 177 207 270 103

Panel C

Received dispenser 0.212 0.452** 0.0567 -0.0336 0.240(0.284) (0.212) (0.120) (0.107) (0.208)

Constant -1.340 -0.689 -1.163 -0.847 -0.764(2.66e-08) (0.275) (1.000) (0.131) (0.661)

Observations 103 178 207 270 99

Weight for age z-score

Height for age z-score

Mid-arm circumference for age z-score

Notes: Observations are at the child level. Dependent variables calculated using WHO anthropometric methodology. Sample is limited to children 60 months and younger and excludes children with implausible z-scores as pre-specified in the WHO methodology. Data was collected eight months after rollout. Baseline controls are included in all regressions and consist of: child age, child sex, baseline HAZ, baseline WAZ, baseline MAZ, whether the child had a cold in the two weeks prior to baseline, whether the child had a cough in the two weeks prior to baseline, whether the child had diarrhea in the two weeks prior to baseline, and the number of months the child was breastfed. "Received dispenser" is any household that received a dispenser, pooled over treatment arms. Unadjusted p-values presented. *** p<0.01, ** p<0.05, * p<0.1.

79

Appendix Table 4. Forecasted handwashing performance (1) (2) (3) (4) (5) (6) VARIABLES Number of forecasted handwashing days in the upcoming week Pre-change period Intervention period Full experiment

Anticipation of monitoring 0.230*

[0.124] Anticipation of triple tickets 0.00363

[0.0735] Monitoring intervention 0.0200

[0.0606] Triple ticket intervention 0.0354

[0.0663] Treated household 3.298***

[0.0582] Incentives 3.281***

[0.0759] Monitoring 3.373***

[0.0928] Dispenser control 3.212***

[0.127] Constant 5.726 6.228 6.317 6.366 2.964 2.964

[0.124] [0.0846] [0.0899] [0.0956] [0.0597] [0.0597]

Observations 455 655 2,125 5,451 21,019 21,019

Notes: Observation at household level with forecasts collected approximately twice a month. Respondents were asked during each biweekly health survey: "How many days in the upcoming week do you expect you and your children will wash your hands with soap before dinnertime?" "Pre-change period" represents days -21 to -1. "Intervention period" represents days 30 to 60 for triple ticket households and days 30 to 110 for monitoring huseholds. Full experiment includes only those days for which we have forecasting data, which is days -21 to 110. Control group for column 1 is the group that was not anticipating monitoring; for column 2 is the group not anticipating a ticket boost; for column 3 is the dispenser control group; for column 4 is the standard one ticket incentive group; and for columns 5-6 is the pure control group. Robust standard errors in brackets and clustered at the household level. *** p<0.01, ** p<0.05, * p<0.1

80

Appendix Table 5a. Alternative hygiene measures (1) (2) (3) (4) (5)

Observed hand

cleanliness

Observed nail

cleanliness

Whether handwashing

habit was achieved

Whether household has non-project

liquid soap

Total dispenser presses in 24 hours

Received dispenser 0.0674*** 0.122*** 1.478*** 0.0456*** --

[0.0214] [0.0263] [0.0392] [0.00932] -- Incentives 0.0562** 0.132*** 1.587*** 0.0623*** 0.583**

[0.0273] [0.0344] [0.0476] [0.0116] [0.239] Monitoring 0.105*** 0.108** 1.269*** 0.0158 -0.0164

[0.0381] [0.0436] [0.0729] [0.0165] [0.358] Dispenser only 0.0410 0.0974 1.318*** 0.0165 --

[0.0495] [0.0625] [0.0979] [0.0257] -- Mean of comparison group 1.552 1.179 1.615 0.0548 5.354

[0.0167] [0.0206] [0.0306] [0.00565] [0.188]

Observations 2,672 2,671 2,669 2,670 951

Notes: Observations are at the household level in Columns 1-4 and at the child-day level in Column 5. "Received dispenser" is the pooled sample of incentive, monitoring, and dispenser control households. Coefficients are reported from two separate regressions: the first pools all dispenser households ("Received dispenser" row); the second includes covariates for each treatment arm (Incentives, Monitoring, and Dispenser only). All regressions include village level fixed effects except Column 5, which compares treatment arms across villages. Column 5 has a restricted sample because the outcome variable is only observed amongst households who received a dispenser. Therefore for this column, the relevant comparison group is the dispenser only group. In all other regressions, the relevant comparison group is the pure control. Observed hand and nail clenliness are graded by the enumerator on a three point Likert scale with 1 indicating no visible dirt, 2 indicating some visible dirt, and 3 indicating extensive visible dirt. Whether a handwashing habit was acheived is rated by the respondent on a 5 item scale as follows: 0 = "How? You did not give us soap."; 1 = "No, not at all."; 2 = "No, not yet, but it is growing"; 3 = "Yes, mostly, but still needs time"; 4 = "Yes, definitely, the habit has been established." Robust standard errors are clustered at the household level. *** p<0.01, ** p<0.05, * p<0.1.

81

Appendix Table 5b. Sanitation outcomes (1) (2) (3) (4)

Whether household defecates in open

Whether household treats drinking water

Received dispenser -0.000599 0.00642

[0.0175] [0.0102] Incentives 0.0232 0.00993

[0.0214] [0.0128] Monitoring -0.0434 0.000136

[0.0325] [0.0180] Dispenser only -0.0420 0.000222

[0.0467] [0.0298] Mean of pure control 0.647 0.647 0.0861 0.0861

[0.0119] [0.0119] [0.00696] [0.00697]

Observations 2,672 2,672 2,669 2,669

Notes: Observations are at the household level. "Received dispenser" is the pooled sample of incentive, monitoring, and dispenser control households. All regressions include village level fixed effects. All regressions include village level fixed effects. Robust standard errors are clustered at the household level. *** p<0.01, ** p<0.05, * p<0.1.

82

Appendix Table 6. Willingness to pay for soap at six months(1) (2) (3)

Received dispenser -4.738**[1.935]

Incentive -9.060*** -7.755***[2.303] [2.393]

Monitoring 1.415 -0.681[3.705] [3.706]

Dispenser only 6.011 4.500[5.243] [5.434]

Mean of pure control 55.74 55.74 53.64[1.476] [1.477] [1.439]

Observations 2,750 2,750 2,478

Willingness to pay (Rs.)

Notes: Observations are at the household level. All regressions include village level fixed effects. Robust standard errors are clustered at the household level. "Received dispenser" is the pooled sample of incentive, monitoring, and dispenser control households. Column 3 restricts sample to those households who do not report having non-project related liquid soap in the household during the midline survey. *** p<0.01, ** p<0.05, * p<0.1.

Appendix Table 7. Spillovers in handwashing rates(1) (2) (3)

Days -40 to -30 Days 40 to 50 Days 120 to 130

No. of monitored households -0.00794 0.0162* 0.00830[0.00659] [0.00838] [0.00863]

Mean of comparison group 0.252 0.279 0.230[0.0355] [0.0399] [0.0412]

Observations 1,106 1,165 1,019

Likelihood of use during reported dinner time

Notes: Observation at the household level. Sample is all dispenser control households. Independent variable is the number of monitored households within 1 km of the dispenser control household. All regressions include village and day level fixed effects. Robust standard errors in brackets and clustered at the household level. Comparison group is dispenser only households who have zero monitored households within a one kilometer radius. *** p<0.01, ** p<0.05, * p<0.1

83

Appendix Table 8. Health spillovers

Whether child had any loose stool in

last two weeks

Total days of loose stool in

last two weeks

Whether child showed

any ARI symptoms in

last two weeks

Total days of ARI in last two weeks

No. of dispensered households -0.00220 -0.00576 -0.00234 -0.0286[0.00203] [0.00487] [0.00377] [0.0215]

Mean of comparison group 0.108 0.216 0.275 1.452[0.0162] [0.0385] [0.0270] [0.175]

Observations 624 629 629 629

No. of dispensered households -0.000767 -0.000983 -0.00672* -0.0337*[0.00249] [0.00575] [0.00359] [0.0183]

Mean of comparison group 0.0867 0.181 0.277 1.342[0.00955] [0.0248] [0.0147] [0.0873]

Observations 1,601 1,602 1,602 1,602

Notes: Observations at child level. Sample is composed of the children in pure control households in each type of village (monitoring village or incentive village). Independent variable is the number of households who received a dispenser (monitoring and dispenser only households for monitoring villages; incentivized households for incentive villages) within 1 km of the pure control household. Comparison group is made up of pure control households who have no dispenser receiving households within a one km radius of itself. Robust standard errors in brackets and clustered at the household level. *** p<0.01, ** p<0.05, * p<0.1

Panel A: Monitoring villages

Panel B: Incentive villages

84

Appendix Table 9a: Learning about health (midline data)(1) (2) (3) (4) (5) (6)

Health index type: Incidence Anthro Incidence Anthro Incidence Anthro

Health index -0.00205 -0.0407 -0.00183 0.0277 0.00206 -0.00771[0.0261] [0.0624] [0.0108] [0.0293] [0.00825] [0.0260]

Constant 0.183 -0.212 -0.0485 -0.279 0.242*** 0.0539[0.239] [0.626] [0.0894] [0.226] [0.0782] [0.215]

Observations 154 32 408 100 889 201

Average likelihood of handwashing at dinnertime one month after withdrawal of interventions

Dispenser only Monitoring Incentives

Notes: Observations at the child level; standard errors clustered at the household level. All regressions include village level fixed effects and controls for the average likelihood of washing during dinnertime during the course of the intervention, baseline health index, child sex, child age, number of months the child was breastfed, household occupation, number of rooms, mother's age at marriage, and mother's education. Health index is constructed using Anderson (2008); the "Incidence" index is constructed as a weighted average of the child being free of loose stool or ARI in the two weeks prior to surveying and the number of days she was free of these illnesses; the "Anthro" index is constructed using child height, weight, and mid-arm circumference z-scores. Therefore a higher health index implies better health. The dependent variable is the average likelihood of the dispenser being active during dinnertime over the course of the one month after the withdrawal of monitoring or incentives (the time frame for monitoring is also applied to the dispenser only group). Columns 1, 3, and 5 include all children below the age of 14 years; columsn 2, 4, and 6 include only children 60 months and below.

85

Appendix Table 9b: Learning about health (panel data)(1) (2) (3) (4) (5) (6)

Week 7 Week 8 Week 9 Week 10 Week 11 Week 12

Panel A: Dispenser only and monitored householdsSick in previous week -0.148 0.217 -0.281 0.0617 0.764 -0.0349

[0.217] [0.300] [0.397] [0.361] [0.476] [1.077]Observations 358 341 337 305 236 259

Panel B: Dispenser only and incentivized householdsSick in previous week -0.278 -0.384 0.499 0.870** -0.100 0.371

[0.332] [0.446] [0.403] [0.374] [0.389] [1.048]Observations 578 562 575 497 455 427

Notes: Observations are at the child level and sample is restricted in each specification to those children who experienced a sickness either in the week prior to handwashing observation or the week after handwashing observation (but not both). Standard errors clustered at the household level. All regressions include village level fixed effects and controls for whether or not the child experienced ARI in the week that the handwashing outcome is observed, the total number of ARI incidences up to the week before observation, and the total number of days the dispenser was used up to the week before observation. The dependent variable is the total number of days the dispenser was active during dinnertime during the week of observation.

86

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